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: EFFECT OF YEAST AND ESSENTIAL OIL-ENRICHED DIETS ON CRITICAL DETERMINANTS OF HEALTH AND IMMUNE FUNCTION IN AFRICANIZED APIS MELLIFERA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The following are some minor edits that should be done, mostly to help with readability of the manuscript:

-You use a combination of ‘honeybee’ and ‘honey bee’ in your manuscript – for consistency, just use one. I would say ‘honey bee’ as two words is used a bit more commonly in the literature, but either is fine. Just be consistent (you use ‘honey bees’ on lines 57, 405, and in Figure 1; the rest of the time you use ‘honeybee’).
-Somewhat awkward wording on line 75 with “fatty bodies”. Maybe “accumulated fat bodies” or “accumulated fat body tissue”.
-For line 81, you state that a product of the hypopharyngeal glands (glucose oxidase) is secreted via the salivary glands. The reference you cite shows that other enzymes are secreted by both the hypopharyngeal and salivary glands (such as amylase), but that glucose oxidase is secreted solely by the hypopharyngeal gland. Products of the hypopharyngeal gland are not secreted via the salivary ducts, but secreted through a separate channel, that opens into the mouth onto the hypopharynx (see for example, Deseyn and Billen, 2005, in Apidologie: Age-dependent morphology and ultrastructure of the hypopharyngeal gland of Apis mellifera workers (Hymenoptera, Apidae)). That line should be reworded slightly.
-In the title of the manuscript, there should not be an ‘s’ in oils in “essential oils-enriched diets” – it should be “essential oil-enriched diets”.
-Line 144 needs the word ‘it’: “…feeding experiment because it is widely used…”
-Line 153 should be reworded to: “…and an elevation of 8 m amsl.”
-Line 176 should say “filled”, not “willed”.
-Line 230 should “One pair of internal housekeeping primers was used…
-Line 243 should say “Relative expression levels… were calculated…”
-The Data Analysis sections should ideally state the Type I error rate used to determine significance.
-Line 338 sounds awkward, and should be reworded. Maybe the authors meant to keep it as one sentence: “It can be reasonably assumed therefore that yeasts naturally associated with bee colony food reserves will not diminish the nutritional status or survival of bees when used as food compounds, AS the specific yeast cells density used here exhibited an acceptable effect on bee survival.” In addition, “yeast cells density used here” should be “yeast cell densities used here”.
-Line 432 should say “…promissory source in pollen substitute formulas to maintain Vg at healthy levels” not ‘and’.
-The last panel in Figure 1 says 9 replicates / cage / type of diet. According to the Methods, there were 9 diets, but 3 replicates of each cage or diet. So 9 diets x 3 replicates = 27 cages. Not 9 diets x 9 replicates = 81 cages.
-The wording for Figures 3-7 refers to “the experiment in different feeding treatments” instead of listing it out, like in Figure 2. The Figures do go in order, but their titles should stand on their own, in case a reader only looks at one figure in particular. As such, it would be helpful to use the wording “in a nutritional experiment using enriched diets containing one of five yeast species associated with the bee life cycle or three types of essential oil from L. graveolens” in all figures from 2 to 7.
Experimental design: The first point is a minor edit that should be made for clarity; the other points should be addressed, as they are important aspects of the methods that are either not mentioned, or that seem contradictory between what is shown in the Methods, and what is shown in the Results and Figures:

-Survival is calculated as the proportion of living bees over the total number of bees, not over the proportion of dead bees (line 171).
-This could be an issue with either the Methods section, or possibly something that needs to be addressed in the Discussions sections as a finding, but it seems to be an important deviation from what would be expected (unless I am missing something). For the fat body accumulation data, and the expression data for Vg and GOx (though not proPO), why are the starting values at day 0 so different between the control and all the other treatments? There could obviously be a small amount of variation between the bees used for each cage, but the variation shouldn’t be so high, and it shouldn’t be consistently the control that is higher than all treatments, for all three measured parameters. Unless I am misreading the Methods, or it is not mentioned, wouldn’t the day 0 readings all be on bees that had just been put into the cages, that had not begun to feed yet? Were the bees that went into the 8 treatment cages treated / handled differently than the bees that went into the control cages? Again, unless I misunderstood something, all of the bees that went into the cages came from a mix of brood frames from a mix of parent colonies. So why would the immediately-sampled control bees be considerably different than the other treatment bees at day 0? The day 0 data point should be the same across the cages, and should be the base level from which the control and other treatments could then diverge going forward. Or is day 0 supposed to just be the first reading, after 72 h? In which case, it is not day 0, it is day 3, and the experiment was run for 12 days not 9 (though if that is the case, why is there no feed intake value between days 9 and 12?).
-It is not clear how long the experiment was run for. Most of the figures show that the experiment was run for 9 days. However, Figure 2 shows the survival curves and survival data continuing until day 12. Was the experiment terminated at day 9, or day 12? If it was terminated at day 9, why does Figure 2 show three extra days?
-Were cages incubated? Or only frames used to collect newly emerged bees?
-On line 279, it states that feed intake did not differ between EO treatments and the control after 24 h. However, the Methods describe that feed intake was only measured every 72 h, and that is shown in Figure 3. Did the authors mean that there were no differences after 72 h? Or were measurements taken more often than stated in the Methods and shown in Figure 3?
Validity of the findings: Most of the comments here involve explanations and conclusions drawn in the Discussions section that should be re-stated, fleshed out, or backed up better, though a few don’t seem in line with the studies being cited:

-The three studies cited on line 353 are used to suggest different findings than what are found with the current study. However, the three studies support what was found in this study. Borges et al. (2020) found no significant differences in mortality among treatments, though carvacrol, thymol, and oregano oil treatments all had higher mortality than the negative control, similar to the current study. Maistrello et al. (2008) found the same thing in an 11-day study: no significant differences in mortality among treatments, though thymol had higher mortality than the control. Costa et al. (2010) did not show differences in mortality until past day 16, and thymol had higher survival at that point due to its control of Nosema ceranae. I think this section of the Discussion should be re-written to show that the current study in fact supports the findings of these cited studies.
-In the same section as the previous comment, it would be worth citing the work by Gashout and Guzmán-Novoa, 2009, in the J of Apicultural Research: Acute toxicity of essential oils and other natural compounds to the parasitic mite, Varroa destructor, and to larval and adult worker honey bees (Apis mellifera L.), as they looked specifically at what the authors are talking about here on lines 359 – comparing toxicity of essential oils (including thymol and oregano oil, containing carvacrol) on mites, adult bees, and larvae.
-For line 387, it mentions that the study by Borges et al. (2020) showed no significant differences in feed intake between treatments. Again, it should be more explicitly stated that this is also what the current study found – no significant differences in feed intake, but slightly lower with carvacrol, thymol, and oregano oil compared to the control. In addition, I would say that the conclusion that diets containing these compounds are “not terribly palatable to bees” would probably be better stated as “Diets containing thymol and carvacrol appear to be less palatable to bees” based on the findings of this and other studies.
-The conclusions stated in lines 469 to 471 are a bit far-reaching. I think they could be stated alongside evidence that shows the opposite. For example, the studies by Borges et al. (2020), Costa et al. (2010), and Maistrello et al. (2008) already cited in this manuscript show that these essential oils reduce Nosema spores, possibly despite the reduction in proPO expression that they also cause. The authors could comment on how this could be (for example, these EOs may reduce proPO expression, but could have stimulatory effects on other aspects of the honey bee immune response, such as the production of antimicrobial proteins and/or the proliferation and differentiation of haemocytes). That being said, it is still an interesting finding worth noting, as it could increase susceptibility to other pathogens.
-The finding from the study cited on line 488 does not seem very surprising, considering that GOx is produced solely by the hypopharyngeal glands of adult bees. Presumably, its expression would therefore not be affected in honey bee larvae fed different diets, but could be affected in adult bees fed different diets. Instead of suggesting that this perhaps might be the case (lines 488 and 489), the authors should back that statement up by citing the studies already mentioned that showed it was in workers only, and age-dependent (Bucekova et al., 2014; Ohashi et al., 1999; Takenaka et al., 1990).
Additional comments: A very interesting study, and one that is worth publishing. Other than some minor edits for clarity, and better explanation of the findings with regards to other published work, my biggest concern would be the issues with the Methods section, where there seems to be some discrepancies and missing information to explain what the results and figures are showing. In my opinion, those are important issues to be addressed for the paper to be accepted for publication.

That being said, I think the findings are important to the bee research and beekeeping communities, with regards to feed additives that can help to maintain honey bee health parameters in caged settings. The study also points out the need for future research to examine how these feed additives affect honey bee health parameters and survival when fed to bees challenged with pathogens such as Nosema ceranae.


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: EFFECT OF YEAST AND ESSENTIAL OIL-ENRICHED DIETS ON CRITICAL DETERMINANTS OF HEALTH AND IMMUNE FUNCTION IN AFRICANIZED APIS MELLIFERA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript has improved, and it is written in unambiguous and professional English. However, I included some suggestions (see comments below).
Line 2. Consider rewording “Nutrition is vital for the health and immune system of honey bees…”
Line 9. Consider rewording “the expression of genes related to the immune system “ or to “the expression of genes related to immune responses…”
Line 23. I don’t think you have to delete the word “genes”. Or you could reword to “Expression of Vg, proPO, and GOx was minimally affected…”
Line 45. I suggest adding a comma and delete “which” to read “…, it is synthesized in the insects’ fact body…”
Line 49. I suggest deleting the word “attack” or reword the sentence.
Lines 51-52. Please revise the use of commas in the paragraph.
Line 72. I suggest using the complete scientific names (Varroa destructor, and Nosema spp). Also, did the essential oils worked against the spores of Nosema? To the best of my understanding, the antifungal properties of essential oils could be related to the lipophilic nature of terpens, and the disruption of the cell membrane during the reproductive state of the fungi, which prevents sporulation (Nazaaro et a., 2017 doi: 10.3390/ph10040086).
Lines 75-78. I suggest using past tense for this section.
Line 98. I suggest deleting “involving multiple variables”. Perhaps the authors mean that the biological pathways associated with immune responses could be assessed using a number of markers. I think that is clear with the explanation in lines 102-106.
Line 105. I suggest substituting “more” with “a”.
Lines 109-112. I suggest revising grammar, the sentence is very long.
Lines 204-205. I assume that the food intake was recorded per cage, and that the food intake per bee (considering live bees) was calculated. Please revise the sentence, it is not clear. Also, the survival was not monitored in all the cages?
Line 208-209. I suggest rewording to “…into the cage and the number of living bees in the cage (initial bees) were recorded”.
Line 2016. Please revise grammar. For example: “The time (hours) that the feeders were in the cages was calculated…”.
Lines 254-257. I suggest: “… and the RNA concentration and purity were measured with a…”.
Line 265. I suggest mentioning the name of the reference gene here.
LIne 287. What do you mean by standardizing? Do you mean that gene expression was normalized to the reference gene, and the control group was used as calibrator? I suggest deleting lines 287-289 to read as follows: “Relative expression levels (REL) of the Vg, proPO, and GOx genes were calculated using the comparative CT (ΔΔCT) method (Schmittgen & Livak, 2008). The relative quantification of the target genes was normalized to RPS5 expression.”
Line 299. I suggest “and transformed if needed…”.
Line 318. Perhaps “effective degrees of freedom”
Line 324. Please revise grammar. I don’t think you needed delete “in the”.
Lines 325 and 328. Please revise this section. If you are comparing the treatments to the control, why are you referring to different days in the parentheses? Also, in the other treatments (yeast) in day 5, the median survival time seems lower compared to carvacol and thymol on day 3.
Line 331. Please revise grammar.
Line 334. Perhaps adding a comma after “three,”
Lines 384-385. Please revise grammar.
Lines 491-494. Please revise grammar.
Lines 501-503 . Please revise grammar.
Lines 534-535. If you found no differences in food intake compared to the control, why do you propose that thymol and carvacol are less palatable?
Lines 53-539. I’m not sure what the authors want to say, please rephrase.  Accumulation of lipids in the fat body?  How does that connect to your argument?
Lines 540-542. Please revise punctuation marks.
Lines 555-557. What is the difference between the first and second factor? Are the food resources to metabolize different molecules than lipids and protein?
Lines 568-569. Could the increase of Vg expression be related to the age of the bees and not the food source?
Line 572. If you are referring to the protein, then Vg does not need to be italicized.
Line 591. Please revise grammar: “the immune system” or “immune function”.
Line 602-605. If the expression of the genes was compared to the control and if you used the same type of cages, then you can assume that the differences in the gene’s expression were due to the treatments. It would be helpful if you discuss your results considering the control or specify that you are referring to the overall pattern of gene expression.
Line 604-605. Please revise grammar.
Line 625. Please revise this sentence; proPo enzyme also regulates cellular immune responses.
Lines 632-634. This paragraph is redundant, perhaps you can rephrase or delete this part.
Line 625. Please revise the use of punctuation marks.
Line 648. Minor typo: “were stimulated”
Lines 669-670. The names of genes should be italicized.
Lines 671-672. Please consider “possibly affecting bee health and the expression of immune related genes”.
Line 675. Please consider using “laboratory”
Line 677. Is the first time that you mention “chemical stress”. I suggest rephrasing, and perhaps focus on the purpose of enhancing honey bee health.
Lines 679-680. Please consider “antagonistic potential towards pathogens, like Nosema spp”
Experimental design: The authors responded to the first review, the objectives are clear, and the investigation and methods are described in detail. However, I suggest revising how the statistical analysis is being reported (see comment below).

Statistical analysis and results (For example lines 341-344). Perhaps I’m missing something, but I understand that you used a linear mixed effect model to assess the differences between treatments. Normally, you would use the Type III sum of squares to report the F value, DF, and the p value of the model, in this case the effect of the diet, cage, and the interaction cage*day. If the model is significant, then you use the p-values of the post doc analysis for multiple comparisons to interpret your results. Also, you didn’t mention if a correction for multiple comparisons was done for the post hoc analysis. Why are you reporting F values for each of the treatments (diets)? Why are the degrees of freedom different? Where are you reporting the F values, DF, and p values of the model?
Here is an example of a study that used very similar analysis, perhaps you’ll find it useful (see results for oocyte size; Derstine, N. T., Villar, G., Orlova, M., Hefetz, A., Millar, J., & Amsalem, E. (2021). Dufour’s gland analysis reveals caste and physiology specific signals in Bombus impatien s. Scientific reports, 11(1), 1-13. https://doi.org/10.1038/s41598-021-82366-2)
Validity of the findings: The discussion and conclusion are linked to the authors research and findings, and the authors are being critical about the limitations of the study. I included few comments that could improve or help clarify the Discussion section (see comments in previous section).
Additional comments: I have no further 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: EFFECT OF YEAST AND ESSENTIAL OIL-ENRICHED DIETS ON CRITICAL DETERMINANTS OF HEALTH AND IMMUNE FUNCTION IN AFRICANIZED APIS MELLIFERA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The following are some minor edits that should be done, mostly to help with readability of the manuscript:

-Line 24, the wording around immune system should be changed. Maybe “Nutrition is vital for health and immune function” or “…health and immune system function” or “…health and immunity”
-Likewise, on line 29, “…can enhance genes related to the immune system” or “…genes related to immune function” or “…genes related to immunity”
-Line 39, you need the word genes – “Expression of the genes Vg, proPO, and GOx”
-Line 55, same as lines 24
-Lines 54-56 are a bit too long, and could be broken into two sentences. You could end it at “…determinant of health and immune function.” And start a new sentence “It is synthesized in…”
-Line 57 is awkwardly worded and not very clear. It could be re-worded to something like “The gene proPO is involved in the production of prophenoloxidase, a precursor (zymogen) of phenoloxidase, which triggers the melanization process, a humoral…”
-line 59, remove the word 'attack'.
-line 60, sounds a bit awkward. Could reword to “Glucose oxidase is critical to the inhibition of pathogens in bee food.”
-Line 87, same as line 24
-Line 88, same as line 24
-Line 91, same as line 24
-Line 112, remove the word 'the', just “…known as Mexican oregano”
-Line 113, remove the word 'of', and re-write as “it belongs to the family Verbenaceae”
-Line 158, remove the word 'of', just “to remove excess CO2”
-Line 165, same as line 158, but also remove the word 'the' as well, “to remove excess CO2”
-Line 199, the subheading should include the word 'expression', either “Vg, proPO, GOx gene expression” or “Vg, proPO, GOx expression”
-Line 242, do you mean “…and transformed when needed”?
-Line 265, add 'in the', “…than those in the control (base diet)”
-Line 270, the wording here is awkward, maybe reverse 'daily' and 'consumed', “Average food intake percentage consumed daily by individual caged bees”
-Line 312, you need the word 'treatments' after the brackets, “…in sesquiterpenes (…) treatments than in the control”
-Line 318, same as line 312, you need the word 'treatments' after the brackets
-Line 334, change to “did not differ from the control”
-Line 356, remove the word 'source'
-Line 380, remove the word 'is'
-Line 392-408, in most instances, the word 'feed' should be added before intake “Under laboratory conditions, worker bee feed intake can”. On lines 394, 396, 397, 399, 403, and 405.
-Line 393, add the word 'and', “…stress due to confinement, and artificial feeding”
-Line 436, same as line 24
-Line 459, same as line 24
-Line 461, replace lifetime with lifespan
-Line 493, proPO should be italicized
-Line 498, change “old nurses” to “old nurse bees”
-Line 498, remove the word 'the', “Expression of GOx may be…”
-Line 512, need the word 'considering', “…as is expected considering that these compounds act as…”
-Line 521, reword to: “The adverse effects of the carvacrol and thymol treatments on fat body accumulation, and gene expression of …”
-Line 533, same as line 24
-Figure 4, the title/heading for Figure 4 is a bit awkward. Could maybe be changed to just “Fat body accumulation” or “Percent fat body accumulation”
-Figure 5, in the figure description, Vg should be italicized
Experimental design: no comment
Validity of the findings: The comments here involve a few small things in the Discussion section that should be changed slightly to accurately reflect the studies being cited:

-For line 375, the study by Costa et al. (2010) should be removed, as it did not show lower survival with thymol and/or carvacrol treatment. The other 2 studies (Borges et al., 2020 and Maistrello et al., 2008), however, do show this.
-For the sentence on lines 489-491, your wording suggests that the three sources listed show both a reduction in proPO expression and a reduction in Nosema spores with carvacrol and thymol. However, they only show the latter, while your study showed the former. I would reword this sentence by moving the proPO expression part to the beginning, to make it more accurate: “However, even though carvacrol and thymol reduce proPO expression, Borges, Guzman-Novoa & Goodwin (2020), Costa, Lodesani & Maistrello (2010), and Maistrello et al. (2008) show that they also reduce Nosema spores.”
Additional comments: Other than the minor edits listed here, I think the issues brought up in the first review have all been fixed.


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: EFFECT OF YEAST AND ESSENTIAL OIL-ENRICHED DIETS ON CRITICAL DETERMINANTS OF HEALTH AND IMMUNE FUNCTION IN AFRICANIZED APIS MELLIFERA
Review round: 4
Reviewer: 1

Output:
Basic reporting: The authors responded to the previous suggestions. I included minor revisions for consideration.
Abstract. I think scientific names could be put in parentheses or commas.
In the abstract, the authors mentioned 6 diets with bee-associated yeasts, but there are only 5 listed in parentheses. Perhaps you are considering the control, but you would need to reword.
L57. Correct typo: ‘The proPo gene is involved in the production of prophenoloxidase’.
L66. Are the yeasts isolated from bees, or from hive products (e.g. bee bread, larval food, and honey)?
L84. Perhaps ‘The objective of the present study… ‘
L85. Would it be better to read ‘… of native bee yeasts and essential oils… ‘
L86. Please consider adding a comma after ‘variables’
L136. Please consider adding a comma after ‘diets’
L141. Please consider rewording to ‘The EOs diets consisted of the base formulations enriched with one of the three L. graveolens chemotypes, classified according to their dominant phytochemical compound, and contained no added yeast materials’.
L255. Please revise verb tense ‘We tested..’
L427. I don’t think you can discuss differences between treatments, because you didn’t do multiple pairwise comparisons, please reword. If the authors wish to discuss differences between treatments, I suggest trying a post hoc analysis with multiple comparisons and adjusted p value. It would give more information, type 1 error, and you would be able to compare between treatments, and have a further discussion. You could also include a comparison between yeast treatments and EO treatments. I believe there are some packages that you can use, like lsmeans after running lmer test in R.
L445. I didn’t find Barragan, Basualdo & Rodríguez (2015) in the reference list. I think it was erased from the previous version.
L455-456. I believe previous studies have found that newly emerged bees and adults have fat body tissue, you can check Ramsey et al. (2019; https://doi.org/10.1073/pnas.1818371116). Perhaps a sentence saying that your study confirm previous reports could be included.
L511. Please consider erasing ‘However’.
L518. I don’t think the hyphen is necessary in ’nutritionally dependent’, please verify.
L544. I suggest that the authors revise the ‘Conclusion’ (there is room for improvement); it would be helpful for the reader if the section follows the same order as the manuscript, by pointing out the main and most relevant results on the effect of 1) yeasts and 2) EO on the tested variables.  For example, the sentence of lines 544 and 545 is between arguments on EOs.
Experimental design: The authors gave detailed information about the statistical analysis. Overall, the results, discussion, and conclusion are in line with the statistical findings, but please edit L427-428 (see previous comment). Also, to the best of my understanding the Satterthwaite’s method is used to estimate the degrees of freedom, but not the F and P values (it does not adjust the P value). Please revise the sentence in L257-259.
Validity of the findings: The authors gave detailed information on the statistical analyses, they answered the research question, and the discussion is supported by their findings (please see comment about L427-428).
Additional comments: The manuscript greatly improved, and the previous comments were answered. I still have some suggestions, I hope they help.


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: EFFECT OF YEAST AND ESSENTIAL OIL-ENRICHED DIETS ON CRITICAL DETERMINANTS OF HEALTH AND IMMUNE FUNCTION IN AFRICANIZED APIS MELLIFERA
Review round: 6
Reviewer: 1

Output:
Basic reporting: The authors have responded well to the previous suggestions. I only found minor typos or suggestions:
L260:  ‘The analysis was based…’
L263-264: Please revise grammar. For example: ‘Dunnett test was used to compare each treatment to the control, and the Kenward Roger’s method to approximate degrees of freedom.’
L277, 278, 280, 285, 287, 289, 295, 296, 298, 302, 303, 309, 310, 312, 315. Please revise the spelling of ‘Dunnett’ test throughout the manuscript.
L348:  ‘to quantify’
L390.  I suggest citing the reference before the comma. For example (i.e. Day 0; Ramsey et al. 2019).
L392: ‘… most of the examined bees…’
L401-402. Please revise grammar. For example: ‘Thus, the expression of Vg gene and vitellogenin synthesis can be nutritionally regulated using protein-rich diets’.
L422-424. Please revise grammar and include why further data is needed (to have a structured sentence).
Experimental design: The authors gave detailed information about the statistical analyses and edited the manuscript considering previous suggestions. The results, discussion, and conclusion are in line with the statistical findings.
Validity of the findings: The discussion is supported by the findings of appropriate statistical analyses.
Additional comments: I suggest that the authors do a final check for typos and grammar.


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: BIOMETRIC INDICES AND POPULATION PARAMETERS OF THREE POLYNEMID FISHES FROM BATANG LASSA ESTUARY OF EAST MALAYSIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. The MS relatively comfortable and smooth with text and discussion.
2.  Needed an enrichment of background-related data-poor of fisheries management.
3.  Figure relatively good, only bit correction in scale and legend and figure performance.
4.  The novelty of this research also found in the text

The improvement in body text related to making any explanation between each other parameter finding.
Experimental design: 1.  Related to journal aim and scope
2. This research found a complementing of research gap related species and data.
3.  Technical and ethical standard fulfilled
4.  Needed any enrichment information on methodology (see comment).
Validity of the findings: 1.  The finding of the research found in the text body, only need enrichment on discussion process.
2.  Statistical analysis clearly follow the methodology
3.  Conclusion stated and clearly
Additional comments: After read and follow the author's idea in MS, I found that the manuscript is interesting and close related to the journal.  The manuscript needs a minor revision (enrichment in body text) to make it concise and faithfully.  I agree to publish and continue to process


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: BIOMETRIC INDICES AND POPULATION PARAMETERS OF THREE POLYNEMID FISHES FROM BATANG LASSA ESTUARY OF EAST MALAYSIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The use of English language is generally fine, although it would benefit from slightly more language revision to improve clarity and correct a few mistakes e.g.
line 32: remove italics from "were"
line 47-48: change to "The estuary is a dynamic ecosystem..."
line 98: change to "cod-end"
line 96: what does "pre-contact" mean?

The main comment I have about the basic reporting is about the figures, which have much information in them that is not explained. I ask the authors to please add more detail into the figure captions so the reader can understand all of the features on the figures, e.g.

Fig. 3: what do the dashed lines, the red lines, and the points represent exactly?

Fig. 5: it would be useful to repeat here exactly what a high or low K value means for a fish?

Fig. 6: what do the black and white bars represent, and what do the blue lines represent, and how were the curves calculated?

Fig. 7: What do the different coloured points in the graphs represent? Please write somewhere exactly what the variable is on the y axis without acronyms.

Fig. 8: why are most bars dashed but the last one is white? Please write about this in the figure caption.

Fig. 9: these graphs are unclear, please enlarge them. Please explain what the two black lines represent, and what the red, green and yellow lines represent.

Fig. 10: how were the curves here (in red) calculated? and how was it concluded about the multiple recruitment events for (b) and (c)?

Also please make the graphs easier to read by using a larger text. And in Figure 2 delete "frequency" text and the black square from the inside of the graphs.

Lastly, line 189-191: I am not sure the categories used here, and in Fig. 5, are so useful. I think a frequency distribution for each species using equal categories would be more useful to describe on lines 189-191 and to display in Fig. 5. For example, maybe on Fig. 5 there is a large percentage of fish with K of exactly 1.01, which would mean they actually are very close to being proportional and should not be grouped with fish that have K=1.3 or 1.4. If equal categories are used on the x-axis then this will represent the data more accurately.
Experimental design: The study does not include any statistical experimental comparisons and aims to describe the properties of populations of three fish species using measurements from samples collected by fishermen. This is only a basic kind of information but may be useful for regional fisheries management and for researchers of the biology of these fish species, so in that sense it is filling a knowledge gap.

The methods generally appear to be described well but please provide some details about how long the nets were deployed during each monthly sampling (line 95-96).
Validity of the findings: The main comment I have is about the lack of conclusions or speculation. I think the discussion needs to be largely re-written, as currently large section are simply repetitions of the results, in some cases using the same sentences, e.g.

line 223-224: this is the same information as from the results, it does not need to be repeated here.

line 243-244: this has already been repeated two times before, it does not need to be mentioned again here. Please mention this fact a maximum of one time within the main body of the manuscript.

line 248-260: again most of this paragraph is a direct repetition of information from the results.

These are just a few examples. Please, I ask the authors to go through the entire discussion and delete any mention there of data or results already provided.

After this repeated information has been deleted from the discussion, it could be better written with some synthesis of general patterns from the results and commentary. One specific example of the kind of changes that could be made is to state why there may be a double recruitment peak for P. melanochir, but only a single peak for other species (line 308-310)? Some more general suggestions about similar changes could be to state how the results could be used to improve the fisheries industry? For what reason might there have been differences for the different fish species? For any unexpected results, what could be speculated as the reason? etc.

Lastly, the conclusions from the study are derived from applying fisheries-related formulae to the measurements of fish taken by fishermen. There will be many assumptions made when applying these formulae and many outcomes (e.g. mortality, exploitation ratio etc.) are all estimates, so I think a section should be added to the discussion where the uncertainty associated with this approach is made clear.
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: BIOMETRIC INDICES AND POPULATION PARAMETERS OF THREE POLYNEMID FISHES FROM BATANG LASSA ESTUARY OF EAST MALAYSIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: A little bit to correction about limit reference point (LRP) of exploitation rate (source of the standard LRP 0,5)
Experimental design: No comment
Validity of the findings: No Comment
Additional comments: Please check and add references for LRP (Exploitation rate over or under 0,5) to make a decision


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: BIOMETRIC INDICES AND POPULATION PARAMETERS OF THREE POLYNEMID FISHES FROM BATANG LASSA ESTUARY OF EAST MALAYSIA
Review round: 2
Reviewer: 2

Output:
Basic reporting: Here are some more instances where the use of English language needs to be slightly improved:

line 46: change to "as one of the world's mega diversity centres"

line 48: change to "a part of the outfall of the large catchment river"

line 50: change to "are an important fishery resource"

line 64: delete the extra ;

line 84: change to "significant lack of studies on growth"

line 166: change to "this is a routine that reconstructs"

line 229: change to "showed"

line 266: change to "mentioned here". On the next line, change to "co-efficient"

line 332: add a space between "and" and "3.8cm"

line 340: remove italics from "and"

Figure 10 caption: please clarify the 3rd sentence here which is difficult to understand currently.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Most of the comments I made in the previous review have been addressed to at least a small extent. It is good to see the details in the figures well described now in this revision.

Much of the repetition of specific results/data in the discussion has been removed as I suggested in my last review, but there is still more of this occurring than normally is included in a scientific manuscript, so the authors could put some more effort into summarising and discussing the implications of results, rather than using large sections of text to just show again the various mean parameters for the three fish species, which were already shown in the results text and the results graphs.


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

Input:
Title: THE BENEFICIAL EFFECT OF PHYSICAL ACTIVITY ON COGNITIVE FUNCTION IN COMMUNITY-DWELLING OLDER PERSONS WITH LOCOMOTIVE SYNDROME
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is written in a clear and concise manner, and is generally easy to follow.

One important difficulty for me while reading the text was the differentiation between excercise and physical activity. On line 94-97, the authors seem to make a clear distinction between the two, but after this both terms are used interchangeably. If excercise is actually defined as "planned, intentional, ....physical activity" it may be questioned how this was measured in this research. As far as I know an activity tracker tracks all PA throughout the day and night and does not provide details on planned/intentional PA. Consider adding this as a limitation or making this differentiation more clear.

Second, while reading the discussion it seemed like a lot of new information/literature references were mentioned that were not yet presented in the introduction. For instance the  paragraph on line 258-271 - i would suggest to mention some of these details/insights already in the introduction and keep it shorter in the discussion (keep line 266-271).

Line 247-248: authors should be careful in not mixing up light physical activity and sedentary lifestyle, which are two different and independent parameters. There is a difference between a person who is sedentary and a person who is physically inactive. Being 'physically inactive' means not doing enough physical activity (in other words, not meeting the physical activity guidelines ). However, being 'sedentary' means sitting or lying down for long periods.
Experimental design: My biggest concern is that the actual problem statement / research aims were not sufficiently clear to me after reading the introduction. I would suggest to revise this and make sure the research questions are linked to existing gaps in the current literature.
All necessary material are in there, but I feel like it needs some restructering and better linking of the different parts, systematically building up to stating the aim of this work at the end of the introduction.
For instance:
- line 57-58, maybe try to link this some more to other research or numbers showing that LS is an important condition to attend to
- line 74-77, I would suggest to revise the wording and motivate why it is important to examine this based on previous evidence or literature (gaps) rather than saying "we thought it would be effective".

Second, I think more details are needed on the measures included to assess the main variables. Especially for the activity registration, LS status, and measure of cognitive function.
- line 143-144: please provide more details on this procedure of data extraction, what is an IC card reader an how is it used, which data can be extracted from this device and how were they processed (i.e. how were raw data transformed in average Ex data?)
- line 154-161: please provide more details on the specific subdomains of cognitive function measured by this scale. Later, in Table 6, these are mentioned but seem to come out of the blue and need more information/details to explain how these were measured in the methods section. Consider adding example items.
- line 165-167: it would be useful to have a better idea on the actual questions that are part of this survey. Consider to provide them in a table or give one example item per domain.

Finally, it is not clear why depression status was measured as this is not motivated in the introduction or research questions, and authors do not discuss it in the results section or discussion. I wonder if authors could tell me why this was the case and how this is an essential variable.
Validity of the findings: Authors could consider to discuss potential threats to internal validity of their findings. That is, specificy the experimental design and how this affects causality inferences.
Specifically, as no control group is includeid, it is not possible to say if cognitive improvements were caused by the excercise program or potentially happened spontaneously over time or caused by other factors. Authors should consider to discuss this limitation.

Also, necessary information is missing on how participants were recruited. Authors could consider to discuss their sampling strategy and additionally mention how this relates to and may hinder the external validity of their findings. I'm specifically concerned about the potential big differences in cognitive function at baseline in this group. In the method section it is mentioned that people with severe congitive issues were helped by a family member, but this makes me wonder how much people differed in terms of cognitive function at baseline (also within the LS or non-LS group) and if this might have influenced effects/improvements. I'm concerned about potential ceiling effects in those already functioning well at baseline (how much improvement is possible over 13 weeks in those doing well?). People with dementia were excluded, but what about people already showing mild cognitive impairments at baseline?

In general, in the discussion, I miss clear links with the original research questions. Please consider to start the discussion with a short recap of the aims and link the discussion of the results to them throughout the text. Same holds for the part on statistical analyses (line 172-193).

I think authors should be careful with using too much speculation in the discussion. Especially the interpretations about the links with pain sometimes seem far-fetched, as no results are reported on pain levels in this group. If this is such an important outcome, I would suggest to report specific results of the pain item and analyze how this relates to excercise and cognitive function instead of making assumptions based on a composite Locomo score which reflects more domains than pain alone...
Additional comments: I think this is a very interesting paper reporting on the links between physical activity and cognitive function in older adults with locomotive syndrom. This paper is well-writen with and generally easy to read. In times of a growing older population with rates of dementia rapidly increasing, it is worth looking how lifestyle behaviors such as physical acitivity might help to prevent this. Overall, findings will contribute to a growing body of literature on this topic. Yet, I have outlined some minor and major comments and concerns that - if addressed - might potentially help to improve the structure and flow of the paper.


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

Input:
Title: THE BENEFICIAL EFFECT OF PHYSICAL ACTIVITY ON COGNITIVE FUNCTION IN COMMUNITY-DWELLING OLDER PERSONS WITH LOCOMOTIVE SYNDROME
Review round: 1
Reviewer: 2

Output:
Basic reporting: The title, abstract, introduction, methods, results and discussion are appropriate for the content of the text. Furthermore, the article is well constructed, the experiments are well conducted, and analysis is well performed. The figures are relevant, high quality, well labelled and described.
Experimental design: The angle of the research is original and the research is within the scope of the journal. Research question is well defined, relevant and meaningful. The overview and their proposal for a more suitable technology is highly technical, ethical and logistical.
Validity of the findings: The introduction is comprehensive. The findings are meaningful. Odds ratio is an appropriate measure to estimate the association between an exposure and an outcome in this study. The conclusions are well stated and relevant to the research questions.
Additional comments: This observational study investigated the efficacy of daily physical activity on cognitive function in older
persons with locomotive syndrome (LS). The authors recruited 70 community-dwelling older people with and without locomotive syndrome and measured their physical activity. The authors found that daily physical activity of 2.29 METs·h/day or higher was important for improving cognitive function in LS populations.

Editorial Criteria
BASIC REPORTING
The title, abstract, introduction, methods, results and discussion are appropriate for the content of the text. Furthermore, the article is well constructed, the experiments are well conducted, and analysis is well performed. The figures are relevant, high quality, well labelled and described.
EXPERIMENTAL DESIGN
The angle of the research is original and the research is within the scope of the journal. Research question is well defined, relevant and meaningful. The overview and their proposal for a more suitable technology is highly technical, ethical and logistical.
VALIDITY OF THE FINDINGS
The introduction is comprehensive. The findings are meaningful. Odds ratio is an appropriate measure to estimate the association between an exposure and an outcome in this study. The conclusions are well stated and relevant to the research questions.

Overall, I think this observational study is novel and will be of interest to others in the community of cognitive disease and depression research. This study is a case control study, whose major strength is that it can provide rapid and useful information on a smaller sample size. This research paper does an excellent job demonstrating the significant difference between the group of LS participants with and without daily physical activity. In general, the work is convincing except some major and minor comments below:

Major Comments:

Due to the long course of follow-up, was there any loss to follow-up for the 70 participants? If so, how did the authors deal with this major challenge and potential source of bias?

Was the reassessment of exposure status required in this study? Do you think it is needed?

Minor Comments:
I’m wondering how the period of 13 weeks was decided?

How did the author decide when to evaluate depression and cognitive function? What if the LS has a long latency period between an exposure of physical activity and outcome?

I recommend adding a flowchart to demonstrate the study design.


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

Input:
Title: THE BENEFICIAL EFFECT OF PHYSICAL ACTIVITY ON COGNITIVE FUNCTION IN COMMUNITY-DWELLING OLDER PERSONS WITH LOCOMOTIVE SYNDROME
Review round: 2
Reviewer: 1

Output:
Basic reporting: Small commment. The authors mention MCI on p.6 (line 168) but as this is the first time to use this acronym, this should be written in full (Mild Cognitive Impairment).
Experimental design: Please provide validity and reliability information with each of the measures described in the Methods sections. This is missing for the activity meter, GDS-15 and ACE-R.
Validity of the findings: Although authors have made considerable changes to the Discussion, I'm still missing links with original research questions / aims / hypotheses and conclusions about wheter or not expectations are (not) confirmed by the findings. I still believe that this section would benefit  from this additional information. For example: "This study aimed to investigate XX, this was (not) confirmed by the findings..."

Also, I wonder if authors could elaborate some more about the absence of a link between exercise and cognitive function in the non-LS group. One could expect that physical activity has a positive influence on cognitive function in this population as well.  Could authors elaborate on the "other factors" that might improve cognitive function in this group on p. 9, line 305.  Additionally, could authors elaborate on potential other reasons for the absence of this link?

On p.9, line 314: it is strange to say that the content of the measured physical activity was "a little unclear". Please revise wording. Also, could authors elaborate on the effect this might have had on the interpretation of your results.

On p.9, line 316: it is not clear what is suggested with "equalization of cognitive function", could authors make this statement more clear?

Finally, the conclusion at the end of the paper is very brief. Consider to add information on the implications of the findings and more specific directions for future research here as well.
Additional comments: no comment


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

Input:
Title: THE BENEFICIAL EFFECT OF PHYSICAL ACTIVITY ON COGNITIVE FUNCTION IN COMMUNITY-DWELLING OLDER PERSONS WITH LOCOMOTIVE SYNDROME
Review round: 2
Reviewer: 2

Output:
Basic reporting: As for the second version, the content is more comprehensive. The whole article is well constructed, the experiments are well conducted, and analysis is well performed. The figures are relevant, high quality, well labelled and described.
Experimental design: The angle of the research is original and the research is within the scope of the journal. Research question is well defined, relevant and meaningful. The overview and their proposal for a more suitable technology is highly technical, ethical and logistical.
Validity of the findings: The introduction is comprehensive. The findings are meaningful. Odds ratio is an appropriate measure to estimate the association between an exposure and an outcome in this study. The conclusions are well stated and relevant to the research questions.
Additional comments: This observational study investigated the efficacy of daily physical activity on cognitive function in older persons with locomotive syndrome (LS). The authors recruited 70 community-dwelling older people with and without locomotive syndrome and measured their physical activity. The authors found that daily physical activity of 2.29 METs·h/day or higher was important for improving cognitive function in LS populations.

Major Comments:

Due to the long course of follow-up, was there any loss to follow-up for the 70 participants? If so, how did the authors deal with this major challenge and potential source of bias?

Response: This is a valuable point. At the start of the intervention, there were 98 people, but data from 28 people could not be used midway through the study (16 were unable to participate in the study for some reason, 9 had incomplete data, and 3 had a daily activity level 7.0 METs·h higher [lines 130–136]), so finally, data from 70 people were analyzed. The purpose of this study was to target people who were living independently in the community, not to impose particularly intense physical activities, so 70 people were considered to meet that purpose. In addition, individuals with high physical activity (7.0 METs·h) greatly exceeding the suggested target amount were excluded from the analysis.

	Feedback: Thanks for the clarification. It totally makes sense to me.

Was the reassessment of exposure status required in this study? Do you think it is needed?

Response: Numerical values such as those for body composition parameters were measured using an instrument, so no reevaluation was necessary. For the evaluations of LS, ACE-R, and GDS-15, the errors due to differences in evaluators and the timing of responding to the questionnaire were small, so we considered the obtained results to be highly reliable. Thus, we think that no reevaluation is necessary.

Feedback: Thanks for the explanation, I agree with you that the reassessment is unnecessary in this case.

Minor Comments:
I’m wondering how the period of 13 weeks was decided?
Response: This decision was made with reference to a previous report on improvements in cognitive function in community-dwelling older after a 3-month exercise intervention (lines 114–117).
Feedback: Thanks for the information. I think it would be better if you could say sentences like “according to the previous study, we decided that ...”

How did the author decide when to evaluate depression and cognitive function? What if the LS has a long latency period between an exposure of physical activity and outcome? I recommend adding a flowchart to demonstrate the study design.
Response: Thank you for pointing this out. All assessments were made before the start of the intervention and after the 13-week intervention. The effects of physical activity were clarified by dividing the participants into non-LS and LS groups before the start of intervention and then comparing the evaluations between the two points. A flowchart is now shown in Figure 1.
Feedback: Thanks for the clarification. It would be more clear if the authors could add it to the discussion section, since readers may raise these kinds of questions. The flowchart looks good to me. Thanks for making the plot.


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: HLA ALLELES MEASURED FROM COVID-19 PATIENT TRANSCRIPTOMES REVEAL ASSOCIATIONS WITH DISEASE PROGNOSIS IN A NEW YORK COHORT
Review round: 1
Reviewer: 1

Output:
Basic reporting: Quite difficult to interpret what was done and how, on which patients. I felt this really weakened the submission. While it is not the easiest subject material to report on, I found it almost impossible to interpret.
At least two pertinent references were not include - very recent references are included so it is not clear why these were omitted as they appear to link in v well with this current work:
HLA-B*15:01 is associated with asymptomatic SARS-CoV-2 infection Danillo G. Augusto, Tasneem Yusufali, Noah D. Peyser, Xochitl Butcher, Gregory M. Marcus, Jeffrey E. Olgin, Mark J. Pletcher, Martin Maiers, Jill A. HollenbachmedRxiv 2021.05.13.21257065; doi: https://doi.org/10.1101/2021.05.13.21257065
And
Langton, DJ, Bourke, SC, Lie, BA, et al. The influence of HLA genotype on the severity of COVID-19 infection. HLA. 2021; 98: 14– 22. https://doi.org/10.1111/tan.14284
Experimental design: I am unclear as to exact patient selection, comorbids etc. Whether this is all in the Overmeyer paper or not I am sure - it needs to be represented. Given the relatively small numbers of subjects the diagnoses and comorbids are going to be extremely important.
Definitely needs a review from a statistician with well defined, appropriate expertise. I routinely deal with HLA data and I found this very difficult to manage.

Admission to study was based on symptoms/clinical presentation – then the two groups were distinguished by a positive or negative COVID test? What was used to determine covid positivity? Am I interpetting this correctly?

Is there a background population control group?

Could the authors explain more clearly how the HLA imputations compare to gold standard next generation sequencing?
Validity of the findings: I am sceptical though open minded. Needs further statistical review.
Discussion needs to be greatly improved, needs to be more focused in my opinion.
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: HLA ALLELES MEASURED FROM COVID-19 PATIENT TRANSCRIPTOMES REVEAL ASSOCIATIONS WITH DISEASE PROGNOSIS IN A NEW YORK COHORT
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is written in unambiguous, professional English.
The literature references are given for a sufficient background of the study. Only lacking are the genetic studies reporting negative findings for an association between HLA and COVID-19, which are in this case the studies with the best statistical power.
The article is well structured, and the tables and figures in the main manuscript represent the main findings in an appropriate way.
The raw data comprises a publicly available dataset, which is properly cited. The supplementary figures and tables would need improvement. For more details see the line by line comments in the general comments section.
Experimental design: The paper presents original primary research about the genetic association of HLA in COVID-19 on a publicly available dataset.
The research question is well defined and relevant but already studied with inconsistent results by several articles as also discussed by the authors. Additional to the discussion points mentioned by the authors I would like to highlight that the majority of the so far published studies is underpowered and results might in at least some cases be based on genetical stratification due to improper sampling rather than on true signals. Unfortunately, the same might be true for this study. The studied dataset is a mixture of ethnicities and the controls also showed symptoms compatible with COVID-19 infection and therefore might be genetically biased from healthy individuals.
Therefore, at least a correction for principal components is highly recommended if there is genetic information outside the HLA Region available. A stratified analysis only on European samples was performed but considering the strong differences in allele frequencies even within single countries and the mixed ethnical background in the present cohort, I expect the correction to be insufficient. Further, the statistic is bend to a limit by reducing the n for a Bonferroni correction based on an allele frequency and correcting for the single loci.
Validity of the findings: Currently I see the main information in the discussion only, where the authors point towards the inconsistency in the so far published papers regarding this topic. I criticize that the introduction gives the impression that the association of HLA with COVID-19 is already well defined and throughout the paper none of the negative findings in this field is cited.
Regarding their own findings the authors bend the statistic for Bonferroni correction by reducing the number of tests by considering only high frequency alleles and studying each locus independently.
Anyway, the conclusions are well stated and discussed.
Additional comments: Line-by-Line Notes:
L.34: “it is established that certain HLA alleles are disease determinants” – So far, all studies I am aware of with a positive finding are clearly underpowered and do not reproduce each other, while the big studies fail to identify any association (e.g. Shachar et al., 2021 and Ellinghaus et al., 2020). You also discuss this point later in the discussion. There were high expectations in HLA analysis but so far, no convincing association has been found.
L.87: Citation 15 does is not related to COVID-19. Further, the big genetic studies showing negative results for the HLA region (even after additional analysis because of expectations in this region) are not listed.
L.90: What is the relevance of the method used in the last paper at this place?
L.116: Maybe it would be nice to include a short note here as well on how you defined the HLA allele in case of disagreement between the models.
L.120: The term “frequency” is misleading, as you are not using the commonly used definition of frequency.
L.133: How is the patient/allele abundance rank defined?
Notes on the Figures Tables and Supplementary Material
•	Fig1/Fig2: n samples for each curve
•	What is the meaning of age :y for sample SRX9033804 (Table S1/S2)?
•	Why are there 103 COVID samples in the Table S1/S2 but only 100 in the manuscript?
•	Why is there only one allele per patient for each class II locus (Table S2)?
•	What is the line in the Supplementary Figure S1? A linear regression does not make sense as the x axis shows an index.
•	A summary of the ethnicity is given in the main text but no information in the listed data.


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: HLA ALLELES MEASURED FROM COVID-19 PATIENT TRANSCRIPTOMES REVEAL ASSOCIATIONS WITH DISEASE PROGNOSIS IN A NEW YORK COHORT
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors clearly improved the manuscript compared to the initial submission. Some uncertainties regarding bias in the data and resulting analysis remain.

Single small suggestions for language improvement:
Line 96: "... we report on HLA alleles with potential analytic (DPA1*02:02) and prognostic (A*11:01, C*04:01) value ...": For me the meaning of analytic and prognostic was not clear in the beginning even if the caption of Figure 2 clarifies the meaning. Maybe more descriptive words like susceptibility and severity/hospitalization free days might improve the understanding.

Line 176-179: I needed to read the sentence several times to figure out what the meaning of the values is. Maybe it would be an option to either split the brackets with the corrected p values into two or to name the n with something like "rank" or "#alleles".

Line 223-227: I would suggest to change the order slightly:
We note that the ethnic background of the Overmyer et al [27] cohort is heterogeneous, and individuals of possible European ancestry represent 45.1% of the COVID-19 positive cohort and  37.9% (11/29) of its DPA1*02:02 subset. In contrast, Asians represent only a minority of the cohort (1.9%) and its DPA1*02:02 subset 3.4% (1/29).

Figure 2: "for each HLA-I and HLA-II alleles" -> allele should be singular

Figure S1: Sentence fragment: "... consistency across."
Experimental design: Line 224: Why are the percentages in the COVID-19 positive cohort (n=100) no full percentages?

Table S1: I think it is suspicious that the only two COVID-19 positive Asian samples have adjacent sample IDs and similar age. This might be a hint for a bias in the dataset as both individuals might be of the same household or social network. Therefore the question if it is sure that no relatives are included in the dataset as this is a very strong bias for all genetic associations that should not be ignored. I would at least add a note to the discussion in case you cannot make sure that no relatives are included in the cohort. Even if no genetic association is noted as the COVID-19 infection spread mainly in clusters  this is another (less important) bias as social networks are to some degree correlated to genetic background.

Table S2: Column names A1 / A2 confusing for people not in the HLA nomenclature esp. in comparison to Table S3.

Table 1/2: It would be great if you could also add the corrected p values for a better overview.
Validity of the findings: The points regarding weaknesses made after the first review were well addressed. But I recognised that no information was given about possible relatives in the dataset (see also 2. Experimental design)
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: HLA ALLELES MEASURED FROM COVID-19 PATIENT TRANSCRIPTOMES REVEAL ASSOCIATIONS WITH DISEASE PROGNOSIS IN A NEW YORK COHORT
Review round: 3
Reviewer: 1

Output:
Basic reporting: NA
Experimental design: NA
Validity of the findings: NA
Additional comments: I have recently suffered a family bereavement. I have read through this study as quickly as possibly as, despite me writing to Peer J to explain my circumstances I have been sent this again for review.
The authors have failed again to carry out an adequate review of the literature.
They have treated low resolution HLA typing as equivalent to high resolution studies and they have again interpreted the findings of references 23 and 24 incorrectly. If they were to re review the raw data presented in these two studies they would find agreement with their own study.


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: CHARACTERISTICS AND FACTORS INFLUENCING THE NATURAL REGENERATION OF LARIX PRINCIPIS-RUPPRECHTII SEEDLINGS IN NORTHERN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Clear  English used throught,  enought literature for background, Good structrue and figures and tables
Experimental design: clear research question, and correct research methods
Validity of the findings: no comments
Additional comments: The natural regeneration of Larix principis-rupprechtii is still a problem in northern China. Understanding natural regeneration is important for forest management, thus your study could be interesting for the associated reader. The authors used the point pattern analysis to illustrate the relationship of seedlings and adult trees of L. principis-rupprechtii and then, analyzed the potential factors that affect regeneration. This seems to be of significance to the instruction for sustainable management of natural regeneration in mountains of northern China. However, there are several minor problems need to be explained and modified.
1. What is the historic vegetation cover of the GDM and why is it a target for afforestation efforts?
2. Why was L. principis-repprechtii chosen for afforestation project in this region?
3. The diversity indices you mentioned in the results could not be found in methods. For example, you mentioned the undergrowth vegetation and litter, but it was unclear what methods did you use. I suggest explicitly starting how you sampled the herbaceous community, diversity indices and litter indices you used to assess.
4. In the objectives you should mention your target species. The first two hypothesis/questions have been answered for other tree species, as you can see from the literature. The third objective can be removed or changed to "identify other environmental factors affecting natural regeneration..."
5. In the Method section you have to clarify whether you study natural forests or plantations. Were these forests recently thinned. Are these forests managed and/or burnt?
6. Please check the labelling of Fig. 2. You might have switched trees and seedlings. I thought seedlings would be more abundant.
7. I’m concerned with the location of litter and herb samples in plots. Are samples taken next to each seedling and adult trees?
a. line 123. Authors mentioned in M&M that the study was carried out in the summer of 2020. Please indicate the date of the start and the end of the field samplings.
b. line 140. How many litters and herbs did you sample?
8. The authors indicated litter and herb effected the regenerated seedlings; it is unclear that how to influence regeneration. Authors stated only some presumption in term of the seed germination but these were not confirmed by examinations or scientific references.
9. In addition to some descriptive sampling methods, you use the word “significantly” in line 229, please add p-values or effect sizes in Fig. 5.
10. Dong et al (https://doi.org/10.1007/s40333-018-0004-3) have shown that the function g(r) has more disadvantages compared with the function O(r). it is suggested that the author should consider the function with better performance here.
11. Generally speaking, the relatively distance between seedling and adult tree effect regeneration, soil nutrient and light are limited; from Fig. 2, some adult trees are distribution in plots, however, the authors use the g12(r) illustrate the relationship between seedling and adult trees, it is unclear that which one does it represent g1 and g2; in Discussion, the authors mention the scale of 1.5-4 m between seedling and adults can promote natural regeneration. Whether the scale is correct.
12. Keywords should not be the repetitions of the title words, please find words which are not in the title, this way search engines of the web will find your manuscript with higher probability.
13. Summarizing the constituents of the common vegetation would be favorable in a tabular form.
14. Please clarify whether the floristic composition survey was conducted by the authors or not? If not, please indicate the source of the data.


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: CHARACTERISTICS AND FACTORS INFLUENCING THE NATURAL REGENERATION OF LARIX PRINCIPIS-RUPPRECHTII SEEDLINGS IN NORTHERN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript named “Characteristics and influencing factors of the natural regeneration of Larix principis-rupprechtii seedlings in northern China” submitted by Zhao et al. conducted the interesting work regarding to the spatial patterns analysis of Larix principis-rupprechtii seedlings natural regeneration in North China forest ecosystems. Its aim are novel and important to reveal the factors which are mainly responsible for the natural regeneration of Larix- the important afforestation tree species in North China for future study. The results sound very interesting and novel. However, I still have severely major concerns with the experiment design itself and some severe flaw also for the writing importance particularly for its introduction and discussion sections if they can induce to the robust and solid conclusion from the current experimental design.
Experimental design: The current descriptions of experimental design, in my opinion, are not efficient to introduce a clear results. e.g. What is the exactly size of selected random plots? Why you selected in the beginning for 40 plots? from the Fig. 1 plot map information, I doubt why selected the plots very close to the uncovered land-system (No. 2 and 3 plots)? which could have great influence on the results of investigation. The M& M section lack of details description for root and litter analysis parts.
Validity of the findings: Conclusion is general ok but is too brief to related to current results.
Additional comments: The manuscript named “Characteristics and influencing factors of the natural regeneration of Larix principis-rupprechtii seedlings in northern China” submitted by Zhao et al. conducted the interesting work regarding to the spatial patterns analysis of Larix principis-rupprechtii seedlings natural regeneration in North China forest ecosystems. Its aim are novel and important to reveal the factors which are mainly responsible for the natural regeneration of Larix- the important afforestation tree species in North China for future study. The results sound very interesting and novel. However, I still have severely major concerns with the experiment design itself and some severe flaw also for the writing importance particularly for its introduction and discussion sections if they can induce to the robust and solid conclusion from the current experimental design.
e.g. the introduction section, the author only focused to introduce the importance for Larix in GDM area, which was too regional to be suitable to expand the results to more interesting audiences.


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: CHARACTERISTICS AND FACTORS INFLUENCING THE NATURAL REGENERATION OF LARIX PRINCIPIS-RUPPRECHTII SEEDLINGS IN NORTHERN CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: excellent
Experimental design: correct
Validity of the findings: Conclusions are well stated
Additional comments: I am generally satisfied with this version of the manuscript revised by the authors. The quality of this work has been substantially improved. I suggest accepting this work for publication in PeerJ.


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

Input:
Title: A DOCKED MUTATION PHENOCOPIES DUMPY OBLIQUE ALLELES VIA ALTERED VESICLE TRAFFICKING
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper describes characterization of docked (doc) mutations in Drosophila. The authors found that one viable allele of doc (doc1) phenocopies dumpy oblique alleles. They demonstrated that the doc gene encodes a protein of Yip family, particularly homologous to Yif1 of yeast, which is thought to play a role in vesicular trafficking between the ER and the Golgi. They further examined genetic interaction of doc1 with a variety of mutants involved in COPII transport and showed that there were synthetic effects with sec23, sec13 and sar1 as well as SyxA and dNSF2. From these and other results, the authors proposed that the phenotype of doc1 was due to the reduced transport of Dumpy protein to the extracellular matrix.
Experimental design: It is an interesting paper. Analysis is mostly genetic and the results shown are just morphology of adult wings, but I enjoyed reading it.
Validity of the findings: There are many puzzles remaining, for example, what is the physical nature of doc1 allele and why only a subset of cargoes are affected, but considering that the precise role of Yif1 has not been clarified even in yeast yet, the findings reported here may be helpful for further understanding of the function of Yip family of proteins.
Additional comments: Before deemed acceptable for publication, I would request the authors to improve the following.

1.	I am afraid the manuscript was not looked over carefully before submission. Typos and missing references were seen at several places.

2.	The discussion is very lengthy. The issues discussed were interesting to me, but many general readers would get tired before reaching the end.

3.	In Introduction (line 35), COPII was indicated as coatamer (should read coatomer) protein complex II, but this is not correct (Wikipedia is wrong). Coatomer is the name originally given by Jim Rothman to the complex of subunits of COPI. COP stands for “coat-protein complex.”

4.	The authors examined genetic interactions of doc mutations with SNAREs, Synaptobrevin (syb) and Syntaxin (Syx) (line 228 and after), and showed some interactions with SyxA. As there are several distinct sets of SNAREs, the authors should indicate which syntaxin it is. According to the model they propose and also considering the roles of Yip family of proteins in yeast, this particular syntaxin should correspond to the Syntaxin-5 of mammals and Sed5 of yeast. Is it correct?

5.	The gene product of dumpy is indicated as Dumpy, Dpy and Dp. It is confusing.

6.	The reference Wang et al. (2018) (line 190) cannot be found in the reference list.

7.	Typo (line 211): Sec1 -> Sec13

8.	What is the ref needed for ZP (line 532).


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

Input:
Title: A DOCKED MUTATION PHENOCOPIES DUMPY OBLIQUE ALLELES VIA ALTERED VESICLE TRAFFICKING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is very well written and is very clear.  There are no major concerns and the minor concerns could be addressed by a re-examination of existing sequencing data and a few straightforward crosses and sequencing reactions.

minor points:

1) Line 190.  Although Wang et al 2018 is cited in text, the reference does not appear in the “references” section.

2) Even though the authors state the all images are the same magnification, there should be at least one scale bar for each figure to show the size of the wings.
Experimental design: Generally solid design and well executed.

Minor suggestions:

1)  Re the doc[99] allele/chromosome.  Unless I missed it, the authors don’t discuss the possibility that doc[99] is a small deletion.  They present evidence that the chromosome has both a doc mutation and a closely linked lethal, which supports the hypothesis that doc[99] is a small deletion that takes out doc and at least one adjacent essential gene.  This hypothesis could easily be tested in two ways:
     A)	The authors could test if doc]99] complements amon, the gene two genes to the left of doc, and to lerp, about 100kb to the right.
     B)	Although the authors state the need for a doc+ chromosome to get DNA for sequencing the doc[99] allele might obscure the presence of a mutation, the need for a doc+ allele might very well reveal the presence of a deletion.  Because balancer chromosomes chromosome diverged from common stocks many decades ago, when sequencing heterozygotes such as doc[99]/TM3 there will be polymorphisms visible as overlapping peaks every couple of hundred bases pairs in intronic regions, and reasonably often in wobble bases of coding sequences.  If the sequenced DNA amplified from heterozygotes doc[99] lacks double peaks for the doc locus, but shows such peaks for a distant control gene, then doc[99] is a likely a deletion.  What might be especially fortunate here is that there is a good chance that doc[16] might have been isolated in the same screen as doc[99] and may have the same parental chromosome as doc[99] and thus could be used to identify polymorphisms to examine in the doc[99]/balancer sequence.  The authors are encouraged to look closely at their existing sequencing data for evidence that doc[99] is a deletion.

2) Fig. 1 and Methods.  Please briefly describe how is wing length measured.  Just the longest line, or as would be more typical, from one landmark to another landmark? If landmarks were used, what landmarks?
Validity of the findings: Conclusions are well supported, alhtoughs some stats are in order for wing length comparisons.

Minor points:

1)	Figure 1M and line 140.  “ … producing a significant further reduction in wing length (Fig. 1).”  The results look highly significant, but appropriate statistical tests should be performed with resulting p-values stated in in text, labeled on Fig. 1M and included in the raw data supplemental table.
Additional comments: This paper identifies the genetically- defined gene “docked (doc)” as being encoded by CG5484, which is the Drosophila homologue of the conserved vesicular transport protein Yif1.  Intriguingly, the doc[1] allele causes a wing phenotype that is strikingly similar to the phenotype caused by some mutations in the ECM ZIP domain protein Dpy. The authors characterize several doc alleles for their genetic interactions with the Dpy, as well as mutations in secretory pathway components and other genes trafficked through the secretory system, including components of the Notch signaling system.  These analyses provide significant insights in to the function of doc in a multicellular organism.

The presented analysis is broadly interesting to researchers studying secretion, ECM, and organ morphogenesis. The authors do a nice job of considering the role of doc in secretion in context of the interactions with dpy, which is an enormous protein that uses a specialized trafficking pathway, and more conventional proteins such as the notch pathway.  Although the authors were scooped in the identification a Drosophila Yif1 homolog (Wang 2018), this in no way detracts from the presented story since the Wang paper focuses entirely on neural functions of Yif1, and does not identify Yif1 as being the gene affected by the doc mutations.  Further, there is no consideration in the Wang paper of ECM, wings or the role of doc/Yif1 in trafficking large cargo.  Thus this manuscript makes important independent contributions to the understanding of the role of Yif1 in secretion and organ morphogenesis.


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

Input:
Title: THE EVALUATION OF FACTORS AFFECTING ANTIBODY RESPONSE AFTER ADMINISTRATION OF THE BNT162B2 VACCINE: A PROSPECTIVE STUDY IN JAPAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors of the study evaluated antibody responses to The BNT162b vaccine in HCW who received the vaccine in Japan. The data is important as there is limited data amongst different ethnic group, so it will add to this body of literature. However, I have several concerns that I am listing below for your consideration. One major limitation are the models used for the analysis. They need to be carefully considered and represented.

1-	In general, I was able to read the paper and understand what was being said, however having said, there are some areas where the sentence construction could be improved upon. For example the background (sentence 100 and 101). I might phrase this as "factors that promote or suppress antibody production post vaccination include obesity, age, sleep duration etc" and then proceed to discuss the studies. Similarly in the discussion, instead of stating a large number of facts it would be important to discuss what the authors want to take away from their paper.
2-	Appears to be referenced properly, however, numbering of references would be easier. Perhaps this is no a requirement of the journal
3-	Raw data was shared, however, as far as the ethical approval is concerned, I did not note a signature on the English version, perhaps the Japanese version was signed.

Specific points

Under study setting and population
Line 127- Cases with new COVID-19 infection after vaccination- is there a time frame for this.
Line  141- was there any validation done about the self-reported BMI?
Line 143- What is the definition of liver disease
Line 146- smoking history (was pack year captured)
Line 147- What is the definition of alcohol habits (were the number per day/week captured)
Line 148- States quality of meal (was this meant to be sleep)
Line 149- what is the definition of outdoor activity for thsi analysis
I think since a lot of this data is self-reported it should be mentioned as a limitation

Regarding statistical analysis-
This is a major limitation of the paper as I think there is an issue with over-adjustment with multiple variables included in the model. Hence I think the regression analysis should be repeated with a succint set of variables that are non-collinear. For example blood sugar and HbAiC are likely to be collinear and yet they are both adjusted for in this model, would it not be more relevant to use clinically relevant cut-offs (such as <5.7, 5.7 to 6.5, or >6.5, or whatever values are used in Japan to define DM and glucose intolerance)
Some of the variables evaluated in the model have such few numbers it appears that the dataset  does not have the power to examine these variables for example cancer, autoimmune disease, liver disease, anticaoagulant therapy, immunosuppressive drugs, immunoglobulin (what is immunoglobulin therapy referring to, convalescent plasma/monoclonal antibody administration against SARS Cov2?).
Similarly for the laboratory tests utilized there appear to be limited rationale to examine for example why hb and hct in the same regression analysis, it appears to me that all of the variables were put into a model and examined. Instead, the authors should critically evaluate what is relevant to their outcome and include these variables.
With 94 participants in the LABG group (it appears that you should be adjusting for only 10 to 12 variables at the most).
I am not sure if the results will hold in a relevant model. These analysis should be re-examined.

In the regression analysis (Reference classes are not mentioned). For example for BMI groups what was the referent group. All the values mentioned have an Unadjusted OR which is not 1.0. Similarly for alcohol what is the referent group, so for example compared to what is the value 1.31 (no alcohol?). All of the referent groups should be clearly outlined in the table

Results-
i-	Could the authors provide a description of the distribution of titers post vaccination by relevant age groups, this is an important aspect that seems to be possible with the data collected (perhaps evaluate based on median age distribution)
ii-	There is no data on adverse reaction profile of the  vaccine- was this captured this seems like a relevant piece of information to include to evaluate if the adverse effect profile of the vaccine is similar among Japanese HCWs

Discussion
Lines 221 to 223- I think the discussion should consider differences between the current study and those cited, rather than merely presenting numbers and concluding that the vaccine responses are similar. For example the Walsh et al article compared differing does of BNT162b vaccine (10, 20. 30 mg), whereas the vaccine under EUA is the 30 microgram dose, which is what I presume was used for the study (which should be mentioned in the paper). In the Walsh et al article, the S1-Binding antibody responses varied according to the age of the participants and also according to the dose of the vaccine.  The authors suggest that the median antibody titers were 9136 U/mL after 28 days, but this number applies to those aged 18 to 55 years who received the 30 micrograms of the BNT162b2 vaccine. Also the mentioned level of 0.6 U/mL in the Walsh et al paper was in the 18 to 55 years of age who received the 30 microgram dose and this was before administration of the vaccine, so it is unclear to me how this value can be compared to the value (7 to 21 days after the administration of the vaccine). Further, the assays used in the two studies were different. So, I think these nuances need to be explained in the discussion. I think the important message here is that the antibody responses are better after the second dose of the vaccine, also in my read they appear to be poor after first dose, barely above the detectable level in the figure) suggesting that a strategy of a single dose of vaccine will be unsuccessful in this population.  Further the discussion talks about median antibody titers but the figure represents the mean titers. Did they mean to say “mean” titers?

Lines 233- I think this should say “older age” the term age should be qualified. How is the age term used in this paper should be discussed
Line 235- I did a quick pubmed search using the terms “obesity and antibody responses to covid vaccines” and I was able to find articles on this (examples- https://pubmed.ncbi.nlm.nih.gov/34109307/) so I am not sure this statement is entirely accurate or perhaps I am misunderstanding what is being discussed.
Line 249 to 250 – as previously stated I am really unable to understand what some of the reference categories are for the analysis
Line 259 to 261- Why are we discussing triceps thickness when the site of injection is the deltoid
Line 268 to 271- this could be an issue with multiple adjustments too. As above this is an issue that should be rectified.
Line 277- Consider stating as “we age”. What is older for this study, I could not figure this out from the table, is the regression analysis based on every year increase in age or every five or every 10?
Line 304 to 310- I think the authors should clearly state where they hypothesize that they are hypothesizing reasons for their observed association, it appears to me that the authors are hypothesizing that the observations associated with no outdoor activity and lower antibody responses is related to vitamin D levels. Do they have banked serum that they can use to explore this association?
Line 334- By stating CD4 lymphocyte activity, are they meaning T cell responses to vaccine, if so they should correct. Also neutralization antibody levels were not examined which is a limitation of the paper.
Experimental design: As above. I feel the model should be re-run
Validity of the findings: In my opinion, the statistics has some serious issues as discussed above.
Additional comments: No additional comments


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

Input:
Title: THE EVALUATION OF FACTORS AFFECTING ANTIBODY RESPONSE AFTER ADMINISTRATION OF THE BNT162B2 VACCINE: A PROSPECTIVE STUDY IN JAPAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: Ok
Experimental design: Sample size is low and no new findings
Validity of the findings: Statistical backup needed
Additional comments: No new finding generated from this data
Only antibody titers wont be sufficient for evaluation of vaccine in population other CMI studies needs to be performed


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: REDUCING PUBLICATION DELAY TO IMPROVE THE EFFICIENCY AND IMPACT OF CONSERVATION SCIENCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: This study explores publication delay as a very important issue for practitioners and scientists, which causes so much headache and frustration. The authors use a huge and good-quality database to explain how publication delay changes over years and is affected by targeted species groups and their threat status, publication types and subjects. The paper is well written, methodologically sound and using sufficient background to support the authors' results. The authors describe the structure of publication delay and propose a useful pathway to reduce it without compromising the quality of science.

Below I suggest some ideas and comments on how this nice study could be improved and enriched.

The language is good, just some minor changes are needed:

Lines 44-45 – delete (time from completing data collection to publication) as this explanation is already given above
Line 46 – change “focussed” to “focused”. Add “significantly” or “marginally” to “smaller delay” to make it more informative
Line 61 – change “decision making” to “decision-making” throughout the text
Lines 69-70 – the sentence sounds incomplete and should be re-worded
Line 154 – change “in “unrecognised journals” ” to “an “unrecognised journal””
Lines 171-172 – this sentence is unclear, please explain or re-word: Any publication source that explicitly stated that it was a scientific journal was categorised as an ‘unrecognised journal’.
Line 194 – delete “will”
Line 197 – do you mean January 2001 to December 2001 or January 2003 to December 2003, to keep them within one year?
Line 216 – the categories of “Management of captive animals” and “non-journal literature” were set to the zero value of the beta slope as redundant, not set as the intercept, because models produce their own intercepts by default
Line 231 – add the comma after “To do this”
Line 233 – add “the” after “within”
Line 314 – change to “(Fig.S2), there were inconsistent, but significant differences in publication delay between”
Lines 348 and 365 – change 3.5 to 3.6
Line 425 – change 2.7 to 3.7 for recognized journals
Line 448 – change “etc.” to “and other duties”
Experimental design: The study design is appropriate. I have just several questions:

I am not yet convinced how the authors identified unrecognized journals. I have checked their list in supplementary Table S2 and found it to contain such well-known and respected journals as Galemys and South African Journal of Wildlife Research. Some other readers would possibly find other reputable journals on this list.

Peer review is applicable not only to journals (which of course would make a majority), but also to books and chapters. How did the authors categorize them in this case?

Why did the authors use Poisson and quasi-Poisson GLM if the response variable (publication delay) is not a count statistic? Tukey test has been used as a post-hoc test for normal data, but as the authors used quasi-Poisson, the data were assumed to be non-normal. Also, Tukey test is a kind of parametric t-test, and I have seen t statistics also in supplementary files describing the results of quasi-Poisson analysis. Please, explain this.

The Methods part is lacking information on how the performance of GLMs was assessed: p values, 95% CI of beta around the zero, odds ratios? I think the AIC-based model ranking would also be useful to see which factors of synopses, publication types, years, etc. are best to explain publication delay.
Validity of the findings: The results are valid and well explained. Here I would like to make the following suggestions:

The Results section contains many references to supplementary files, yet the key numbers are not indicated and the reader would have to jump to supplementary files and back to follow the track. This is not convenient. I would suggest to add some numbers to Results to make reading smooth – e.g., in lines 297-301 to add publication delay estimates for the periods 1912-1980, 1980-1990, 1990-2000 and 2000-2020.

Line 263 and thereafter – please write the ranges of p values, not p<0.05, p<0.01 etc.

As to me, information about publication delay between different IUCN statuses is one of the most important messages of this study, but it is hidden mostly in Table S9 which is big and out-of-the-way. I would suggest to re-make Table S9 as a series of heat maps in the main text showing different colors for different intervals of Tukey test statistics. This also can be done for other Tukey tests in the paper. I am just advising to dig out important information from supplementary files and move it to the main text.

Also, it would be important to add more numbers in Abstract, such as publication delays +/- error for captive animals, non-journal vs. journal publications.

Original eps files of figures were not labeled on axes and therefore were not understandable. I found fully prepared figures only in the pdf file of the submission. Is this a journal regulation or there is some other reason?
Additional comments: The paper is very interesting, important and timely, and I thank the authors for it. Here I would like to express some more thoughts which the authors could consider adding to this study.

Delays can be caused by journals because they fail to find suitable reviewers or even handling editors, even by the journals having numerous editors in their editorial boards. From my experience, keeping a manuscript for about half a year at the stages of “editor assignment” or “under review” is not uncommon and possibly even becomes a routine now during the pandemic times. As reviewers are not paid, they have little motivation to respond and meet deadlines. This can be particularly relevant to publications on conservation effectiveness which require multidisciplinary knowledge and skills from reviewers (ecology, study designs, statistics) and may experience particular delays in publication time because suitable reviewers can be unavailable or unknown to editorial boards. Again from my experience, several times I was asked by journals to recommend my colleagues who could have a capacity to review the effectiveness papers. This is also an indicator that effectiveness is a new topic for conservation which should be widely promoted in science and practice.

Publication delay adds to a delay of waiting for funding between the time when a project is submitted and the time when it is approved (this also can be a research topic). This makes conservation practitioners spend much of their time for waiting of published knowledge and/or money.

Apart from reluctance and long time required to publish, a strong disincentive to publish is insufficient knowledge of English. Such authors perceive rejections as a personal tragedy and may refuse to submit later on. I know that Oryx helped the scientists from developing countries to write scientific papers, but I do not know if it works now. Such initiatives are essential.

Conservation effectiveness does not fit many journals and the re-submission delay can be particularly long. A rapidly growing number of new journals focused on practical conservation (Ecological Solutions and Evidence, Conservation Science and Practice, Frontiers in Conservation Science) may reduce publication delay. If the journal Conservation Evidence had an impact factor, it would also help stimulate submissions.