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: SMRT SEQUENCING OF THE FULL-LENGTH TRANSCRIPTOME OF THE WHITE-BACKED PLANTHOPPER SOGATELLA FURCIFERA
Review round: 1
Reviewer: 1

Output:
Basic reporting: On the whole, the article is clear and unambiguous with professional English used throughout. However there are some sections which require further clarification ( listed below).

The article is self-contained with relevant results to the hypothesis.

Sufficient field background/context is provided. Some statements made require literary references though.

The article has a professional article structure. The CCS and Unigene sequences have been made available to the public. Release of the subreads would be greatly appreciated.

Figures
Figure 1: Unsure if it is just me, but after multiple attempts of downloading the figure, the title and axis are not loading properly and are instead being replaced with empty boxes.
Figure 2: Legend on plot could be changed to indicate what is being presented. Also underscore should be removed from z-axis title
Figure 3: Legend missing
Figure 4: Good
Figure 5: Good
Figure 6: Legend can be more descriptive of each plot. Concerned there is too much detail being present within one figure requiring the reader to zoom in to read the font

It would be extremely beneficial if a roadmap figure was provided to the reader describing the pathway the sequences took from subreads all the way to annotated transcripts

Tables
Table 1-3: Good
Table 4: Needs description below table

Comments on specific sections of the article

Line 41-42: Description is unclear on the two ways WBP affects crops. The term ‘wind burning’ is used but I am not sure of its definition and searching it online did not return an answer. I looked up the papers referenced and neither mentioned this term, closest I found was ‘hopper burn’.
Line 45-46: This information can probably be moved closer to the beginning of the introduction.
Line 74-75: Third-generation sequencing is long read sequencing. Saying third generation sequencing is SMRT sequencing is misleading as SMRT sequencing is a proprietary method owned by Pacific Biosciences. For example, Oxford Nanopore is another third-generation sequencing method.
Line 79:82: Citation is needed for these descriptions of read lengths and potential benefits of using intact high-quality long transcripts.
Line 83: Should change SMRT to SMRT sequencing.
Line 95: What and how many inbred strains were used.
Line 117-120: Description of cDNA generation should be reworded for clarity.
Line 124-131: The description of “ANGLE” does not make sense to be included under the library construction section. Additionally, the description of “ANGLE” contains almost identical wording to the abstract of the publication which originally described it.
Line 157: What parameters were used?
Line 158: The “ANGEL” pipeline is a reimplementation of Shimizu et al 2006 “ANGLE” algorithm. “ANGEL” was coded by Pacific Bioscience’s Elizabeth Tseng https://github.com/PacificBiosciences/ANGEL
Line 164: What parameters were used?
Line 190: Citation needed for MISA.
Line 196-207: Whole section is one sentence, perhaps provide more description of each database used.
Line 253-262: How many of the generated coding sequences matched and/or did not match currently known WBP proteins?
Line 270-290: Order of the presented results should match the order of the plots in figure 6. Consider changing order of results or order of plots in the figure. COG results describing functions is hard to follow.
Line 297-298: Prior to this study, were “several” or a significant higher number of full-length transcripts unknown?
Line 300-301: Can you elaborate on how the SMRT sequencing in this study is useful for genome annotation and gene function studies.
Line 304-306: I am unsure what the authors were trying to convey in these lines.
Line 309: Comparison to previous Illumina study results should be introduced in a less abrupt manner.
Line 328-329: Before this study, was RACE the only way to obtain full-length cDNA sequences?
Line 346: Consider using a more accurate or compelling word than “lots” to described the number of transcripts obtained

Special attention should be paid to the different genomics vocabulary used in the manuscript. Several times a term is used which is vague or does not accurately describe the information being presented. Additionally, a quick grammar review should fix a few relatively benign grammar errors.
Experimental design: Goals and analysis pipeline are well described. If possible, providing the code used to run analysis pipeline will greatly increase ability to replicate experiment
Validity of the findings: Results are stated, but the final sequences and annotations are not provided to support the claims. Only the 156,138 generated unigenes are provided with no accompaning annotations.
Additional comments: Nice thorough analysis


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: SMRT SEQUENCING OF THE FULL-LENGTH TRANSCRIPTOME OF THE WHITE-BACKED PLANTHOPPER SOGATELLA FURCIFERA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is generally clear and well-written.  There are no major problems with English writing and grammar, but there are a number of minor wording issues that could cause comprehension difficulties.  There are also some minor problems with figure labels.  I have detailed these issues below with reference to line number.

General comments: It would help to define abbreviations at their first usage in the main text, even if they have been defined in the abstract.

line 75 - the phrase "without interrupting splicing" should be removed

line 77- "assembly" should be replaced with "identification", since transcripts are not assembled with SMRT sequencing.

line 81 - Insert the word "sequencing" after SMRT

line 121 - Information about ANGLE/ANGEL seems to be in the wrong section.  Also, the software used was probably ANGEL (reference the github site), which is based on ANGLE (Shimizu et al 2006.)

line 136 - insert "for" after searching

line 138 - replace "comprised" with "contained"

line 140 - replace "isotypes" with "isoforms".  I believe isotypes refers to classes of antibodies.

line 177 - This sentence should be reworded as follows:  The transcript sequences predicted using Plek, CNCI, and CPC tools were used to search the Pfam-A and Pfam-B databases using hmmscan.

line 192 - remove the word "strict"

line 212-213 - removing low (levels of) artificial concatemers doesn't seem to be related to identifying full-length reads.  This might need to be two separate sentences.

line 218 - remove "consistent"

line 280 - Species are not homologous.  This section should be rewritten as "Finally, the transcripts were compared to those in the NR database.  The species with the most matching transcripts were ….."

It would also be good to comment on whether those are the species expected to be most closely related to S. furcifera.

line 289 - "several" should be replaced with "many" or "most"

line 294 - add "sequencing" after SMRT

line 319 - rewrite the beginning of this sentence to However, until recently, full-length cDNA sequences could only be obtained….

Table 2 - line 7 - replace "consistency" with "consensus"

Fig. 1 - even in the high resolution image the axis labels are not legible.  The characters have all been replaced by small boxes.

Fig. 2 - I would suggest mentioning the color code in the figure legend.

Fig. 3 - The figure legend should include more than just the title.
Experimental design: The research question is clearly stated and the experiment is well thought out and clearly described for the most part.

There are a few sections in the Methods (TF detection, ANGEL, lncRNAs) where it is not clear which set of transcripts (FLNC, non-redundant, HQ?) were used as input for a particular step. This information should be added.

There are also some gaps in the analysis of the transcript data once it was obtained (see Validity of the findings section below).
Validity of the findings: The availability of full-length transcripts for S. furcifera will be a huge help in efforts to annotate the recently sequenced genome. However, I have some concerns about the analysis and interpretation of the data.

1)	There is no mention of classification or mapping of the transcript sequences.  When I accessed the data deposited in the NCBI Sequence Read Archive, the Taxonomy Analysis performed by NCBI indicated that approximately 12% of the transcript sequences appear to be of viral origin.  Unless these transcripts originate from viral genes integrated into the S. furcifera genome, they should be removed from the S. furcifera transcriptome (although they might still be interesting in their own right).  The transcripts should also be mapped against the S. furcifera genome at some point in the pipeline.

2)	The analysis is also lacking an assessment of transcriptome completeness.  The authors should analyze their transcriptome with a metric such as Benchmarking Universal Single-Copy Orthologs (BUSCO).

3)	The number of unigenes (156,138) seems very high compared to the number of non-redundant isoforms reported in insect Iso-Seq transcriptomes of similar scope (Jia et al 2018, Zhang et al 2019).  The authors describe this large number of unigenes as an improvement over previous S. furcifera transcriptomes, which might be the case if this large number was due to an increase in transcript isoforms.  However, Table 4 indicates that the vast majority of the unigenes represent single isoform genes.  It seems likely to me that sequence errors and/or allelic differences are preventing the collapse of the transcripts into the actual number of non-redundant isoforms.  In the Iso-Seq transcriptome papers mentioned above, non-redundant isoforms were either based on the high-quality transcripts (Zhang et al 2019) or a lower stringency level was used with CD-HIT (Jia et al 2018).  Mapping transcripts to the S. furcifera genome could also be helpful in identifying redundant transcripts.  All downstream analysis would benefit from a more accurate count of non-redundant isoforms.
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: SMRT SEQUENCING OF THE FULL-LENGTH TRANSCRIPTOME OF THE WHITE-BACKED PLANTHOPPER SOGATELLA FURCIFERA
Review round: 1
Reviewer: 3

Output:
Basic reporting: Correct gene structure is critical in downstream biological analysis. PacBio Iso-Seq provides solution to sequencing complete gene without need of having any assembly artifacts. This manuscript provides detailed analysis of data generation and processing. Although it lacks analysis to emphasize data quality and usefulness. It also lacks comparative analysis with previously published datasets.
Experimental design: Read correction – PacBio reads have high error rate. Self-correction with Quiver might not be enough. Correction with Illumina reads is critical for getting correct open reading frames (ORFs) for protein-coding genes. Do authors have any way to measure accuracy? One way to monitor progress of correction is look at the length of ORFs or CDS.

Another issue with Iso-Seq is the depth of sequencing. There is chance of missing genes based on coverage along with diversity of transcripts in the stage/tissues used for sequencing. To generate comprehensive transcriptome, combining Illumina RNA-Seq reads based transcripts could lead to more complete representation of the transcripts. To be useful for broader community, authors should integrate public RNA-Seq datasets with Iso-Seq to generate comprehensive transcriptome.

Methods - Library preparation
It mentions about CDS predictions using ANGLE. Seems redundant and out of place as this is also discussed later in the CDS prediction section.
Validity of the findings: lncRNA are important class of non-coding genes. lncRNA are spliced genes and numbers of exons is critical parameters in classifying lncRNA. I would recommend to show mapping statistics to the genome for lncRNA along with the rest of the Iso-Seq transcripts.

Do authors have BUSCO single copy marker statistics for Iso-Seq based transcriptome?
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: SMRT SEQUENCING OF THE FULL-LENGTH TRANSCRIPTOME OF THE WHITE-BACKED PLANTHOPPER SOGATELLA FURCIFERA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The article is clear and unambiguous with professional English used throughout.
There still remains some sections which require further clarification (listed below).
The article is self-contained with relevant results to the hypothesis.
Sufficient field background/context is provided.
The article has a professional article structure.
The  630,447 circular consensus sequences can be found at https://www.ncbi.nlm.nih.gov/biosample/SAMN12612920/

Line 74-77 –  Reorganize sentence to: Single-molecule real-time (SMRT) sequencing, a third-generation sequencing technology developed by Pacific Biosciences (PacBio),  can effectively overcome this problem (Eid et al. 2009; Korlach et al. 2010).
Line 147-149 – Clarify that insecta_odb10 was the dataset used in BUSCO analysis. Should it be transcriptome mode instead of protein mode? Was BUSCO analysis done on the full-length reads, FLNCs, or polished consensus isoforms? This sentence also should be moved to a different location, currently interrupts the flow of the sentences surrounding it.
Line 166-168 – Reorganize sentence to : The ANGEL pipeline, which is based on ANGLE (Shimizu et al. 2006), was used to identify the protein coding regions from cDNAs (https://github.com/PacificBiosciences/ANGEL).
Line 202-203 – Reword sentence to: The unit sizes and their minimum number of repetitions were: 1-10, 2-6, 3-5, 4-5, 5-5, and 6-5
Line 232-233 – This part should be placed next to the description of the reads used in the analysis. It should also be reworded for grammar.
Line 293 – Remove “were”
Line 298 – Change “was” to “is”
Line 299 – Uncapitalize “The”
Line 332 – Change “readings” to “reads” or “transcripts”
Line 334-335 – Change to: The lengths of the FLNC transcripts were aligned to the sizes of the transcriptome library.
Line 332-335 – Confusing switches between singular and plural objects
Line 335-336 – Need to reword for clarity
Line 342 – Change “from Illumina sequencing result” to “assembled using only Illumina sequencing”.
Line 361-364 – Change to “However, most methods used to obtain a full-length cDNA clone are time consuming, expensive, and inefficient (Bower & Johnston 2010; Chen et al. 2016; Schmidt & Mueller 1999).
Line 380-381 – Change to “Through the PacBio SMRT sequencing platform, a large collection of full-length transcripts were obtained.
Experimental design: Goals and analysis pipeline are well described. If possible, providing the code used to run analysis pipeline will greatly increase ability to replicate experiment.
Validity of the findings: Results are stated. The 156,138 generated unigenes are provided with no accompaning annotations.
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: SMRT SEQUENCING OF THE FULL-LENGTH TRANSCRIPTOME OF THE WHITE-BACKED PLANTHOPPER SOGATELLA FURCIFERA
Review round: 2
Reviewer: 2

Output:
Basic reporting: All of my original concerns have been addressed, but a few minor errors have been introduced during the editing process.

lines 125-126.  The following lines seem to be out of place. They may be left from the ANGLE material, most of which was deleted. "During the CDS prediction process, we kept the best sequence as the final result. If there were multiple sequences that could not be filtered, all of them were output."

lines 158-159.  The phrase "which is based on ANGLE (Shimizu et al. 2006)" should be placed immediately after "The ANGEL pipeline".

line 326-327 - Reword to " However, until recently, the methods for obtaining full-length cDNA clones were time consuming, expensive, and inefficient."

line 344 - Replace "a plenty of" with either the word "numerous" or an exact number.

line 345 - Add "as well as" after the comma.
Experimental design: The one issue I still have with the experimental design is the lack of mapping of transcripts to the S. furcifera genome.  The authors responded that they do not have access to the genome, but I was able to download the assembly described by Wang et al (2017) from http://gigadb.org/dataset/view/id/100255/File_page/2.  The BUSCO statistics for the Wang et al genome indicate a high degree of completeness, so a comparison should be very informative.
Validity of the findings: Interpretation of the current findings appears to be valid.
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: COVID-19: TAIWAN’S EPIDEMIOLOGICAL CHARACTERISTICS AND PUBLIC AND HOSPITAL RESPONSES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper provides epidemiological characteristics of the 39 confirmed COVID-19 cases in Taiwan, one of the countries with lower rates of the disease. This is a very informative paper for other countries and needs to be published very fast.
Experimental design: The experimental design is a serial study case, a type of observational study in epidemiology. I think that is important to make this is clear in the manuscript methodology section. It is important to improve the methodology section and inform that it was used statistical descriptive analysis. It is necessary to inform what variables were collected in relation to the patients, such as, age, gender, etc. It is not clear. I know the variables because I read the results section, but this information need to stay in methods as well.
Validity of the findings: This is an important description of COVID-19 cases and health system responses in Taiwan. This is necessary to help and compare with other countries. All of this information is essential.
Additional comments: Line 60 and 61: format the reference.
Line 61: format the date.
Check the numbers formatting according to the English language.
Line 119: change 2019-nCoV to COVID-19.
Line 147: format the percentage.
Table 1: check the formatting and the uppercase of the words.
Figure 3 and figure 5: important to have in the supplementary files or together with the figure, as a panel figure, the traduction to English.
Figure 5, try to improve the pictures, they are distorted.
Line 193, 195, 198, 200 and 203: fix the term facemask.


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: COVID-19: TAIWAN’S EPIDEMIOLOGICAL CHARACTERISTICS AND PUBLIC AND HOSPITAL RESPONSES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Thank you for giving me the opportunity to review this interesting and potentially important manuscript. I found the manuscript to be practically focused on potentially effective control measures to contain COVID-19, and as such could be of use to other countries in the early stages of the disease outbreak.

Regarding your use of referencing, I found this to be adequate. However, as you will see in my specific comments on the attached annotated PDF, I felt there was a need to provide more context from other countries. The major selling point of this manuscript is why Taiwan appears to have been more successful at controlling COVID-19 than other countries, and without direct comparison I feel this might be a missed opportunity.

Regarding tables/figures, these were useful.

A major concern I do have however is your use of English which, whilst generally good, had several points for improvement. I have highlighted a number in the manuscript, but would recommend further detailed proofreading before re-submission.
Experimental design: This manuscript is in scope for the journal. As more of an epidemiological report, I found the methods generally sufficient to describe your approach, though I felt the lack of a clear timeline between case reports and introduction of measures to be confusing in places. I would recommend including a clear timeline of events to improve clarity. It would also be useful to include a scale for the measures introduced, as these more practical details would be invaluable to other countries considering implementing similar control measures.

I would further recommend the authors to carefully review whether various parts relating to 'normal' hospital practice in Taiwan would be necessarily known to those residing outside of Taiwan. I think there could be some value in quickly summarising what normal infection control measures, for example, would look like outside of the unique COVID-19 situation.
Validity of the findings: As a description of measures deployed, I found this manuscript to be sufficient. I further thank the authors for being careful to carefully acknowledge and qualify the fact that an exact causative link between lack of a significant outbreak and the control measures introduced could not be established. I would however recommend further comparison with other countries, as i stated earlier.
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: COVID-19: TAIWAN’S EPIDEMIOLOGICAL CHARACTERISTICS AND PUBLIC AND HOSPITAL RESPONSES
Review round: 1
Reviewer: 3

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: I think the paper is sound, the methods are well described. The results are well presented and are interesting for the reader.
However a minor revision is necessary at least and that would be my suggestion:
Some minor points: the language should be checked and corrected by a native speaker, there are many errors.
Fig.1 (Distrribution of cases and development in Asia is really not necessary, but in any case much to detailed,


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: COVID-19: TAIWAN’S EPIDEMIOLOGICAL CHARACTERISTICS AND PUBLIC AND HOSPITAL RESPONSES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Many thanks for sending this much improved manuscript for second review. It was a pleasure to read, was informative, and as such I think this has now very nearly reached publication standard. I do however have a small normal of minor modifications for consideration just to maximise the benefit of this paper, which I have described below.

Line 41: Consider using 'close contact' rather than physical, to also encompass droplet spread as a transmission mechanism.
Experimental design: I am happy with the presentation of this article - the addition of the timeline does greatly improve clarity, thank you. Just a couple of suggestions here:

Line 138-139: Regarding being moved to isolated rooms upon confirmation of COVID-19, it might be helpful to briefly outline, if possible what the stepdown procedure was for recovering cases i.e. what criteria were there to decide when patients could leave isolation. Deciding when patients can re-enter normal life is a significant area of debate, and one I feel you could contribute too.

Line 148: You have a few citations that are incorrectly formatted. Review these before publication.
Validity of the findings: As above, I am happy with your presentation and interpretation of findings. As such I have only a couple of suggestions:

Line 205: It might improve clarity by more carefully defining 'medical mask' and comparing it with more robust masks, such as N95. I'm guessing you are referring primarily to standard surgical masks here, but it might help to be a bit more specific, if possible.

Line 251: The herd immunity strategy in the UK has largely been abandoned. It might be good to acknowledge that for the reasons you stated why Taiwan did not follow this approach, the UK has now also changed approach... perhaps further justifying your decision.
Additional comments: Many thanks again for the opportunity to review this valuable manuscript. I noted in your rebuttal letter that you asked if I would be happy to be included in the acknowledgements section. Thank you so much for this thoughtful request, I am pleased that my reviews have helped you. I'm not sure if this journal publicly names reviewers anyway (in which case really don't worry), so have raised this with the editor.

Thank you also for the good wishes in the light of this pandemic - I hope you, your co-authors and families also continue to remain safe and well over the coming months.

Best wishes,
David


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: COVID-19: TAIWAN’S EPIDEMIOLOGICAL CHARACTERISTICS AND PUBLIC AND HOSPITAL RESPONSES
Review round: 3
Reviewer: 1

Output:
Basic reporting: Now, the manuscript is perfect.
Experimental design: Now, the manuscript is perfect.
Validity of the findings: Now, the manuscript is perfect.
Additional comments: The manuscript has been improved and looks great!


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

Input:
Title: COVID-19: TAIWAN’S EPIDEMIOLOGICAL CHARACTERISTICS AND PUBLIC AND HOSPITAL RESPONSES
Review round: 3
Reviewer: 2

Output:
Basic reporting: No concerns - I would now consider this work publishable.
Experimental design: No concerns - I would now consider this work publishable.
Validity of the findings: No concerns - I would now consider this work publishable.
Additional comments: Many thanks for this further re-submission. The modifications you have made have further improved the article quality, and I particularly think the addition of your step-down strategy will prove useful. To date, although literature in this area is very fast moving, I haven't heard much discussion of criteria for removal of patients from isolation rooms. It is interesting to note that to my knowledge in my own country (the UK) patients are being moved to normal wards after a single negative test. In my opinion, considering the fairly poor sensitivity of this test, the UK strategy is madness. As such, any prompting of debate about a more cautious approach, such as undertaken by yourselves, is much needed and very useful. However, your acknowledgement of the time taken for patients to on average cross this boundary is also welcome - there are difficult compromises to be made, particularly as our understanding of the duration of infectious potential in patients remains poor. Anyway, I digress, I have recommended this article be published and look forward to seeing it in print! I wish you the best of luck for your continued control efforts, and share your hopes for a future less impacted by COVID-19.
Best wishes,
David


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 SYSTEMATIC REVIEW OF THE DIRECT AND INDIRECT EFFECTS OF HERBIVORY ON PLANT REPRODUCTION MEDIATED BY POLLINATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: This work reviews the literature regarding herbivory and pollination in order to evaluate their effects and influences over plant reproductive success. Despite that to know the gaps and research needs in the field is very necessary, this work do not sustain an original proposal and is lacking of the background needed to suffice as an original publication. Below I comment some points that describe this problem.

1-The tittle, “A systematic review of herbivore-pollinator interactions: theories, methods, and challenges”, do not reflect the content of this ms. This is not clearly about the “interactions of pollinators vs. herbivores” but rather is more focused the influences of herbivory over plant reproduction mediated by animal pollination. The whole work seems to be oriented to understand plant fitness consequences therefore, this must be clearly stated in the tittle.

2-Conclusion paragraph in the Abstract is vague and should provide the main message of this work in a more straightforward way. For instance, line 58-59 in the Introduction and lines 278-279 in Conclusions provides hits on the goals and main findings of this manuscript.

3-Figure 1 is incomplete and inaccurately represents the direct and indirect effects on plant reproductive success due to herbivory vs. pollination. Current figure is only considering the effects from animal foraging on vegetative and floral structures over a “flower” category box. This is not useful to understand the process as the effects of different stresses may influence plant physiology and development, triggering changes on reproductive budget over time that could be reflected in less gametes and floral resources (such as nectar, fragrances, oils etc.) as well as the overall quality of floral display. This figure does not allow to easily discussing these different effects.

4-Plant response towards pollination can also affect herbivory. Several organisms change the sign of its ecological interaction through ontogeny. For instance, many insects are first herbivores (folivores, florivores, gall-inducers, among others) and later, as adults, contribute to pollination. By not considering this connection you loose the chances to discuss on the lack of experimental studies evaluating this kind of ontogenetic switching between herbivorous and pollinator role of several animals and its plant fitness consequences. This is especially important in perennial species.

5-Moreover, a good portion of plant species present mixed mating systems where their reproductive strategy can be heavily influenced by: 1. Effective pollinator visits and 2. Herbivory. Plants may switch towards self-reproduction when they are stressed by the lack of visits by pollinators (that could be due to a loss of attractiveness by florivory) or due to a heavy pressure of herbivores. Your model cannot be applied to a considerable amount of plant species. In Table 3, where authors draw connections between plants and animals associated, there are plant species that are capable of producing seeds WITHOUT pollinators!, such as for example Tristerix aphyllus (Loranthaceae) is capable of asexual reproduction by selfing and even apomixis. This is the most serious drawbacks of this work as the ms. is only considering animal pollination as the source of plant fitness.

6-Introduction: This section is not very well written; authors should drive readers towards their goals.  Mechanisms involved in plant response towards the interaction of animals are very well documented and should be presented using its nomenclature, in a more concise and clear way. For instance, instead of “pre-formed” defenses use “constitutive”. Furthermore, several stresses plants suffer due to herbivory depends on the kind of foraging behavior, taxonomic identity of the attacker and are expressed in varied temporal frames. All these must be explained and considered if this review intends to be systemic. Each of the definition related to this characterization must be provided in this section, or in Table 1 associating the intro with it, besides of categories of foraging attacks authors must define for instance: kind of plant responses (either resistances, defenses, etc.) timing of these responses, among others. For example “complete vs. incomplete florivory” is only mentioned later in discussion.

7-Regarding Methods, instead of using country frontiers for showing where the articles used belong. I recommend authors to use the information regarding the kind of biome where these researches were done. In this way they will be able to inform if there is a bias on the kind of habitat where these research have been done. Moreover, as mentioned above, the temporal frame considered between herbivory versus pollination effects must be considered in the analysis. Preponderance of herbivory damage as well as the abundance of pollinators can depend strongly on biome, therefore, this is an additional issue that is not addressed nor discussed in this draft.

8-JA manipulative experiments should not be classified as “herbivory” as these only considering some aspects of the reactions of plants towards a stress similar to herbivory damage.

9- Concerning the evaluation of papers to be used in this review it seems that there were no filter regarding an adequate taxonomic identification of the animals interacting with the plant species. The quality of animal identification is heterogeneous in the articles selected for this revision. This is not trivial as even organisms belonging to a same genus may display negative or positive interactions with plants. If a better selection of works based on taxonomic accuracy was not possible, due to the reduced number of works, at least this should be commented as an additional issue to be solve by future works.
Similar problems are found in the plant species lists, it would be desirable that plants species name be accompanied by their family classification. This provide additional information to discuss on potential research biases.

10-Discussion. Do not reflect the whole development of this work. For instance only Fig. 1 is referred in this section. Why Fig. 3 is not even mentioned here? There are no original conclusions. Most of what is discussed seems to be extracted from previous revisions such as Garcia & Eubanks, 2019 or Mothershead & Marquis, 2000. It is possible that the lack of meta-analysis, or any statistical tool, in this draft do not allow authors to conclude based on the data complied from this revision. In general this section do not provide new ideas to what has been already published in previous reviews on this topic.

I consider this work do not curated the information used for the revision adequately, and is far from a systemic review on the reproductive effects of herbivory and pollination over plant fitness.  This ms. do take advantage of the massive body of evidences from plant reproductive ecology or chemical ecology approaches that otherwise may have provided a solid background to the bibliographic inquiry here presented. Unfortunately, this does not merit publication.
Experimental design: All comments in 1
Validity of the findings: All comments in 1
Additional comments: No additional comments


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

Input:
Title: A SYSTEMATIC REVIEW OF THE DIRECT AND INDIRECT EFFECTS OF HERBIVORY ON PLANT REPRODUCTION MEDIATED BY POLLINATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The organization and flow of the introduction and discussion were somewhat scattered and not always connected to the main point of the methods.  Some of this has to do with larger potential issues (i.e. what the purpose of this paper is meant to be; see “General comments” below).  But even setting that aside, the organization needs some work.  Paragraphs are frequently long, and jump from topic to topic.  For example, the first paragraph of the paper covers direct and indirect effects of herbivory, the importance of pollination, potential interactions between herbivores and pollinators, and effects on plant fitness; that’s enough information/topics for three or four paragraphs.

There’s also a few language choice problems, including inconsistent use of “direct” and “indirect” (sometimes stated clearly, other times assumed or stated unclearly) and the word “pathways” which seems to have at least three meanings in the introduction (pathways of effect between herbivores and pollinators, different kinds of herbivory, or different classes of interactions such as mutualism vs. antagonism).  Also, the introduction uses the hypothesis in Figure 1 as part of the justification for the paper, but doesn’t ever directly talk about that figure or its implied hypothesis/es.

Raw data have been supplied and are mostly labeled well, though some of the values, abbreviations, and column headings are unintuitive.  For example, using “number of pollinators” = “100” to denote an entire community was studied.  The accessory documents define all of these well enough, but there may be changes that would make the data easier to understand without having to reference additional documents.

I like Figure 1, and I think it could serve as a hypothesis for a path analysis in future research.  However, on two different computer screens the green color used for some arrows was very difficult to tell apart from gray or black; when printed in grayscale, it was even worse.  Figure 4 is very information-dense, which makes it somewhat difficult to parse – but the figure legend explains things fairly well.  Figure 3 was the figure I struggled the most with.  I understand what it’s trying to show (and how), but the lines don’t always connect with the species names and it’s frequently hard to tell what the lines are connecting or pointing to.  It’s also not obvious what order the interactions are listed in; it’s not alphabetical by species names.

The tables in both the paper and in the supplemental documents were hard to tell where horizontal dividers belonged.  Additionally, text in each column isn’t necessarily justified vertically in the same way across rows.  For example, in Table 1, the term “Root Herbivory” is justified higher in the cell than its definition in the next column, which makes it hard to read as a cohesive row.  There needs to be either space between each row or horizontal lines added.
Experimental design: I had trouble deciding what the main purpose or question of this paper was meant to be; see my comments below in “General comments.”  There was very little in the way of experimental design and even less about how the analysis was completed.  The methods section was only one short paragraph long, and focus on how papers were found and sorted, with no information about what data were taken from those papers or how those data were further analyzed.  Overall, methods and results focus mostly on qualitative information, with less interest in analytical or technical information.
Validity of the findings: It’s not always entirely clear how the authors decided which paper goes in which category, especially when it comes to things like simulated herbivory/florivory or studies with multiple species or studies that didn’t measure reproduction etc.  I tried to parse through some of the data based on citations I’m familiar with, and frequently I would have put different data points in their table.  This makes it difficult to know if the summary of what kinds of studies have or haven’t been published is accurate.  I can’t tell if this is a matter of providing consistent, logical definitions for each data choice, or if the data itself are too subjective to be interpreted analytically.

The main conclusion of the paper seems to be that herbivores effect pollinators (directly and/or indirectly) which in turn can affect plant pollination success.  As a conclusion, this feels weak; this is something that is already well known by ecologists in this field, and probably assumed by ecologists in related fields.  Additionally, that conclusion doesn’t tie back to the results in this paper (looking at where more studies are needed, for example).  This conclusion is valid, but it doesn’t serve either the purpose of the paper or the scientific audience of a paper like this.
Additional comments: I’ve read this paper several times through in preparing to write this review.  This general topic is one of great interest to me.  There have been previous reviews that touch on how herbivory and/or florivory specifically affect pollination and (potentially) plant reproduction, but they are all several years old now.  I think there is room to have a review that talks about what we know and what we have left to learn on the topic.  However, I’m not convinced this paper fills that role.

The methods and results of this paper focus on the number of papers published in this field, pointing out what kind of studies are most and least common.  But the methods and results don’t attempt to summarize the kinds of results those papers found.  Meanwhile, the introduction and discussion provide a cursory summary of the results from those papers (as you would find in the introduction section of an original research paper, for example) but doesn’t really put them in the context of how many articles of each type have been published.  This makes the paper feel like two separate things, neither of which is completely satisfying.

I think the authors may need to think about what they’re trying to accomplish with this piece.  If their goal is mainly to point out the gaps in terms of where papers are or are not being published, that can be done in a much more concise manner (a “Note” article, for example) that could summarize the information presented in the methods and results section of this paper as a sort of call to arms for researchers.  This could be of interest to anyone familiar with the field, and might provide a jumping-off point for new research project ideas.  However, an article of that type would need only limited review of results from those previous papers (since the “results” would be how many and what kind of articles are being published); in that case, the information currently in the introduction and discussion of this paper would be greatly reduced to a couple of paragraphs for context.

If the main goal with this paper is to review the results from previous herbivore-plant-pollinator studies, then there should be less focus on how many papers have been published and more focus on what the results of those papers were.  This may or may not include a meta-analysis, if you want a more analytical approach to the data.  Even a traditional review, however, could provide new insights into what the common trends are in this field, with room to point out remaining gaps in our knowledge.  In a review paper of this type, the results and methods section as currently written would go away (though there may be mention of numbers of studies in the discussion) and the current introduction/discussion would need to be expanded and reorganized around common themes in the results from published papers.  As I said before, there have been reviews that do this already for this topic, but they’re all a decade or so old by now, so there’s probably room for a new one – especially if you focus on what’s been added to the literature more recently.

Overall, while there is a lot of good information in this paper, its current format is somewhat confusing and unsatisfying.


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 SYSTEMATIC REVIEW OF THE DIRECT AND INDIRECT EFFECTS OF HERBIVORY ON PLANT REPRODUCTION MEDIATED BY POLLINATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: This version of the ms includes most suggestion proposed, now it is adequate for publication.
Experimental design: This version of the review contains better curated information.
Validity of the findings: This version of the ms includes suggestion proposed; now it is sufficient for publication.
Additional comments: N/A


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 SYSTEMATIC REVIEW OF THE DIRECT AND INDIRECT EFFECTS OF HERBIVORY ON PLANT REPRODUCTION MEDIATED BY POLLINATION
Review round: 2
Reviewer: 2

Output:
Basic reporting: 1.	The introduction is long, a little jumbled, and not quite focused on the same thing as the rest of the paper, and as a result it feels disconnected from the rest of the paper.  For example, there’s more than a full single spaced page of background on just herbivory in isolation, which seems like too much since that’s not the main point of this paper.  I think the introduction needs to be made more concise, with relevant material shifted to the discussion section for more exploration and unnecessary material removed.
2.	The introduction also probably needs to be restructured/reorganized.  You want to give enough background information to directly lead into the topic of herbivory affecting plant fitness by affecting pollinator visitation, and lead up to your purpose in writing this review.
3.	Related, there are a couple of places, especially in the introduction, that still cover several topics in one long paragraph, and probably need to be split up.  For example, the second paragraph in the introduction (beginning at line 50) could be split into three paragraphs:  one paragraph from line 50 to 56; a second paragraph from line 56 (starting with “Most typically…”) to line 67; and a third from line 67 (starting with “In this systematic review…”) to the end at line 72.
4.	Compared to the first version of this paper, there have been significant improvements to content and organization of discussion section.  I especially liked the first paragraph in the discussion.  However, by adding so much material, it’s easy to get lost in all of the details when reading it.  I suggest adding subheadings to split up the material (e.g. “Effects of florivory on pollination” and “Effects of vegetative herbivory on pollination” etc).
5.	Line 354:  “Folivory, root damage, and stem damage were found to negatively impact several floral traits, as well as pollinator visitation and reproduction.”  You don’t really get into the details of what these effects are.  I would prefer to see each of these types of vegetative damage talked about separately, with the kinds of effects on floral traits, pollination, and reproduction that are generally seen.  If there is enough information, they may each get their own paragraph.  If there is little information, they may just be separate sentences in the same paragraph.
6.	Figure 3 is a nice addition.  However, the red dots showing study sites are so small I didn’t see them at first even in color.  In grayscale, they are completely gone.
7.	I still have trouble with Figure 4.  It’s very hard to read, with so many thing lines connecting names in small font, and having the lines behind the text makes the names harder to read.  That said, it is improved from the last version in that I can at least (with some effort) tell which name each line is supposed to connect to.

Smaller comments:
•	In the very first sentence in the introduction (line 50), “Plant fitness is determined by the net outcome of interactions with other species.” – while it’s true that interactions with other species partially determine plant fitness, they aren’t the only thing that affects plant fitness.  Resource availability or abiotic factors, for example.
•	Lines 44-46:  “interactions between two species do not represent the net outcome of relationships” – these are typically called non-additive effects.
•	Line 75:  “rob the plant of resources” – the term “robbing” in the context of plant-insect interactions, especially involving flowers, may be confused for nectar robbing.
•	Paragraph from line 73-85:  in this paragraph introducing types of herbivory that can affect pollination, you talk about complete florivory, but not partial florivory – even though later you say partial florivory was more often studies.
•	Line 169-171:  You say that partial florivory can affect pollination by changing flower symmetry, but that’s far from the only effect of partial florivory on floral display.  Published research has demonstrated partial florivory can affect flower size, color, VOCs, lifespan, sex ratio, nectar production, defenses in flowers, etc.
•	Line 309:  This is a comma splice at the comma between “potential to impact pollinators” and “for instance patches”
•	Line 373:  “directly comparing individual species” – species of what?  Plants?  Herbivores?  Pollinators?
•	Lines 438-439:  This is a comma splice at the comma between “focal herbivores” and “those that looked”
Experimental design: My comments on the design of the previous version were mostly addressed.  My only comments now are:
•	You spend a lot of time talking about complete florivory versus partial florivory, but when you give stats (e.g. line 245, Figure 5) you don’t separate them out.  This might be useful for comparison, especially since (as you point out) most florivory studies focus on partial florivory.
•	I feel like I need to know a little more about your exclusion criteria, since there are a few citations I can think of that seem to measure direct effects of herbivory on pollination that aren’t included in your review.
Validity of the findings: •	The part of your title after the colon (theories, methods, and challenges) doesn’t really reflect your findings or your purpose.  You don’t cover current theories about resource allocation, pollinator selection criteria, or other theoretical frameworks that might have an impact on this topic.  Similarly, you don’t really go over the methods for studies that test these kinds of questions.  Challenges are only obliquely addressed, by pointing out what kind of studies haven’t yet been attempted much.
•	Lines 298-301:  You mentioned compensating for or shifting phenology in response to florivory, but there are also examples of species shifting mating system (i.e. from outcrossing to selfing in plants with mixed mating systems) that led to no overall reduction in reproductive output.
•	Paragraph 363-383:  Another potential explanation for the limited effect of vegetative damage on floral traits etc is that plants preferentially allocate resources to reproduction (since it’s so important), including flowers, and may suffer in other ways instead.
•	You summarize your main findings at the end of the paper twice, in the paragraph beginning at line 448 and in the Conclusions section.  Consider combining them into one conclusion section instead.
Additional comments: The authors’ revisions have, in my opinion, significantly improved this manuscript from the previous version.  In particular, they added a lot more information overviewing previous findings on the topic in the discussion section, which lends itself much more to a review.  However, despite significant edits, the introduction section still feels disconnected from the rest of the paper, and a little jumbled.  The discussion would benefit from subheadings to provide structure.  Revising the introduction may require major revision, but all of the other suggestions I’ve made are intermediate to minor revisions.


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

Input:
Title: AGE-DEPENDENT DIFFERENCES IN IRIS COLOURATION OF PASSERINES DURING AUTUMN MIGRATION IN CENTRAL EUROPE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Capturing birds for ringing purposes is common technique for both amateur and professional ornithologists. While species identity is often easy, ageing and sexing birds in the hand is more difficult, and requires training. Criteria used are most often based on slight differences in colouration and wear between juvenile, post-juvenile or adult feather; hence, an understanding of moult patterns is a key feature for plumage-based ageing and sexing. In this paper, the authors expand on eye coloration differences in dark-eyed passerines as an additional means of ageing.

Eye-colouration as an age criterion is already used for some species with specific eye colors/patterns that changes between juvenile and older birds (such as e.g. barred warbler, golden oriole, lesser whitethroat), but a more general use across passerines is not widely used. To my knowledge, Falsterbo Bird Observatory in Sweden is one of few sites that have used it routinely on a broader set of species. Although written mainly in Swedish journals, I think some of the papers from Falsterbo could be useful for the current study. For data on willow warbler: https://www.falsterbofagelstation.se/arkiv/pdf/304.pdf; whinchat https://www.falsterbofagelstation.se/arkiv/pdf/158.pdf; reed warbler https://www.falsterbofagelstation.se/arkiv/pdf/125.pdf; robin https://www.falsterbofagelstation.se/arkiv/pdf/110.pdf; reed bunting and common whitethroat https://www.falsterbofagelstation.se/arkiv/pdf/111.pdf; tree pipit https://www.falsterbofagelstation.se/arkiv/pdf/157.pdf. These papers generally agree with the premise of the current study: that eye color changes with age and could be an additional criterion for ageing birds in the hand.

In evaluating this manuscript, I was asked to first comment on basic reporting, and then move on to validity of findings and experimental design.

The first of the base reporting criteria relates to language, and in my opinion, your text reads fairly well and it is easy to understand – in most parts – what you have done, and why. However, there are a number of smaller grammatical errors in the text, as well as some scope for increasing clarity, that would render the paper easier to read. For instance, in the text you have not settled on one term for what you study, but use ‘eye colour, iris colour, colour of eyes, colour of irides’. A general overhaul of the text should help to identify these cases; I have not had time to scrutinize language in detail.

The second point relates to context of the paper in relation to the research field as a whole, i.e. how well introduction and background reflects what is known. I am not up to date on all literature on eye colours, but the introduction feels adequate in terms of setting the scene and discussing what has been done previously. With that said, I think the examples from Falsterbo mentioned above should be considered to include for both introduction and discussion.

Of the last basic reporting points, I would like to see a better use of figures. Figures 1-3 of goldcrest eyes are not easy to compare side by side, as the birds are in different angles and the focus on the eyes differs, with some interference of the flash. To a non-trained ornithologist, the difference between the birds in current Figure 3 is not easy to see. High quality, side-by-side picture of the eyes would be a good thing to add for a collection of representative species. If possible, all pictures of species/individuals could be presented as extra material online. In terms of raw data, the authors presently supply an excel file with data. The data is readable, but could be improved by clarifying what the different codes represent. For instance, species names could be written in full (rather than having to guess what turmel is) and you could describe what the values in columns E and K represent.
Experimental design: My comments on experimental design is largely connected to validity of findings, please see under the next heading for a discussion on this. For the base premises of experimental design, I believe that manuscript adheres to the Aims and Scopes of the journal, that research question is defined, but that some additional analyses are needed in order to strengthen the paper (please see below).
Validity of the findings: My main concern is to what extent the current data can be used to suggest that eye colour is a ‘reliable feature for age determination in field studies’ (as you say in the abstract) / ‘reliable mean of age determination to larger set of species than previously described in the literature’(as you say in the conclusions). My first concern with such statements is that it implies that checking the eye colour is on par to plumage-based ageing, rather than an additional criterion. For the species that you list in Table 1, the ageing of birds on plumage criteria is fairly straightforward. For instance, ageing a blackbird as juvenile or adult in autumn is easy on plumage (retained juvenile great coverts, primary coverts, pointed retrices etc), and I don’t see how eye colour would improve this determination significantly in practice. A similar argument could be made for other species in the list.

Second, for the data provided in Table 1, the distribution of class 1 and class 2 largely, but not completely, follows plumage-based ageing, while class 3 is more a mixed bag. Your statistics says the method works well for juveniles, but only in 70% for adult; thus for adults, this method is not really that reliable. My third concern is whether classification of eye colour in the paper can be uncoupled from plumage-based ageing. My understanding  is that one person both aged the birds based on plumage (and skull ossification) and then classified eye colour of aged birds. Unfortunately, this may increase a risk of introducing bias in the data. That is, if a bird has been classified as adult on plumage it may be more likely to get a classification as adult also on the eye colour because of unconscious bias. I would have liked to see how other people would classify different eyes. That is, 1) one person ages the birds according to plumage criteria, 2) takes pictures of the eyes of all birds, and 3) present these photos to others to classify in a blinded way. In such a setting it would be easier to get a measure of how well the two ways of ageing holds up. At present, your hypothesis is very likely correct, but the setup used can not really separate from other hypotheses. If you have pictures, it would be quite easy to test, and I would urge you to do so. It would also be an important resource for other ringers if those pictures and classification was accessible on the web.
Additional comments: I appreciate the opportunity to read this paper, and I hope you find the comments above helpful in revising it. Eye colour as ageing criterion is something that has often been discussed when I have been part in ringing activities, and a thorough guide on how to do this is warranted in the community.


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: AGE-DEPENDENT DIFFERENCES IN IRIS COLOURATION OF PASSERINES DURING AUTUMN MIGRATION IN CENTRAL EUROPE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English is generally good. However, especially in the abstract there are some phrases that I would correct (e.g. in the northern Poland => in northern Poland). But then I’m not a native speaker, so I recommend to give the manuscript additionally to a native speaker for corrections.
Experimental design: Excellent
Validity of the findings: Although I’m not a good statistician, the findings are supported by generally accepted tests, so the validity is good.
However, it should be added in the conclusions that ageing of birds with intermediate iris colour is not recommended.
Additional comments: It would be nice to add the variation of percentage on species level. In the text this could be done in general (varies between …%), in table 1 a column for percentage of reliable aged birds in adults and first-years could be added.
In the conclusions it could be added that these results may enable ringers to age safely not only birds difficult to age by plumage (mentioned), but also for those impossible to age by plumage (not mentioned), namely those undergoing a complete postjuvenile moult.


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: AGE-DEPENDENT DIFFERENCES IN IRIS COLOURATION OF PASSERINES DURING AUTUMN MIGRATION IN CENTRAL EUROPE
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am happy to say that this is a very much improved manuscript, and all my comments have been addressed in a satisfying way.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Again, thanks for the effort made in revising the paper. I think it stands much stronger now, and am happy to endorse it. One thing that puzzled me was that there seemed to be two versions of the abstract in the files sent to me, but I guess it is the correct version in the file that is formatted as a manuscript (and the other probably pasted in at submission portal).


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: TEMPORAL AND SPATIAL VARIABILITY OF TERRESTRIAL DIATOMS AT THE CATCHMENT SCALE: CONTROLS ON PRODUCTIVITY AND COMPARISON WITH OTHER SOIL ALGAE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Manuscript #45133 “Temporal and spatial variability of terrestrial diatoms at the catchment scale: controls on productivity and relation to other soil algae” by Jasper Foets, Carlos E. Wetzel, Adriaan J. Teuling and Laurent Pfister – Submitted to PeerJ. Review report

The authors assessed the variability of terrestrial diatoms over a catchment in Luxembourg, over space (16 sites) and time by conducting monthly sample collections over 1 yr. Diatom species and pigment concentrations were analyzed and correlated with sites characteristics. Based on the references cited in the introduction, it is interesting to see that this subject has not been tackled recently, although it is topical in a context of global change. From the title (“relations to other soil algae”), I would have, however, expected statistical analyses and in-depth discussion on the relationships between algal groups under variable sites and dates, and maybe on the competitive abilities of such organisms in soil environments.

The paper is generally well written. I am not a native speaker but I found it easy-to-read. The abstract provides a comprehensive overview of the study and the obtained results. In the introduction, the authors provide important background information. However, the identification of research gaps is somewhat lacking.
Experimental design: The methods section gives an overview on the analyses made. The study design and the chosen endpoints are relevant. I found some inconsistency in presenting the “Scanning electron microscopy analysis” before having described the sample collection. Consequently in that paragraph, I missed some important information on which samples were analyzed, what the authors meant by “non disturbed soil samples”. Are they the cores described later on (line 150)? Were they fixed? Frozen? Lyophilized? Coated?

Some more details could also be provided in order to be able to reproduce the work. Important aspects I came across are: an overview of the sites’ characteristics could be added (in a summary table within the main manuscript, complementary to the detailed dataset provided in supplementary material), the lack of information on reference substance tests and of description of validity criteria (which are the certified standards you used and what are the detection limits for them?). Is there a reason why you chose Fe and Al as specific metals for analysis (line 181), I this that this should be justified/explained by the authors here. Then you specify that the pH was measured, but was it used to calculate/estimate the free metal ions concentrations? Finally, I have some questions about the statistical evaluation: on which data is the DCA performed? On diatom community composition (as you mention “species turnover”)? This is unclear to me. For diatom biovolume calculations, did you use all diatom species found in the samples, or did you remove rare species below a threshold of relative abundances? In this case please detail.
Validity of the findings: The results section provides a good overview on the results, but I was surprised by the fact that they are described in the present tense, instead of the commonly used simple past. I have a specific reservation on the description of the results made on line 301-302. I think there is an incorrect formulation of the results you observed, linked to the fact that some variables are correlated and of them, some explaining ones are removed. More precisely what I mean here is that I strongly disagree with the following statement “diatoms sometimes had twice the amount of photoprotective pigments […] when the temperature is high” suggesting that temperature is the driving force for this increase in photoprotective pigments. I would rather think that protoprotective pigments are overproduced under increasing incident light (also see what you discuss on lines 336-338 about the photoprotection from incident UVs by higher vegetation height). Parameter which is obviously potentially correlated with higher temperature. I suggest rephrasing this sentence.

The discussion section is compiled following similar organization as in the results. The findings are compared with relevant literature in the field and the section provides a critical assessment of the results and suggestions for further research. I have a specific comment on the biovolume calculations and conclusions drawn (lines 379-384). The fact that you found no correlations can be explained by the methodology used. Indeed, diatom biovolumes were calculated here from literature data, which are an average of the species dimensions published. It is well-known that there is a large range of variability in diatom cell sizes, that may be related to their specific habitat conditions. Maybe they were missed here, and would have been seen using measured dimensions. Could you discuss on this?

The supplementary material provides valuable additional information on the sites characteristics and pigment analyses.
Additional comments: Overall, I think this is an interesting and topical study, fitting well to the scopes of the journal. I recommend to accept it with moderate revisions.

You will find additional specific comments below.

Introduction
Line 64: Be careful with the use of “evolution”. This term usually refers to some Darwinist meaning (e.g. see Forbes, A. A. & Krimmel, B. A. (2010) Evolution Is Change in the Inherited Traits of a Population through Successive Generations. Nature Education Knowledge 3(10):6), maybe prefer a more unspecific word such as “change”?
Line 111: Remove capital to “Soil”
Line 111: How is defined “diatom productivity”? Could you specify here?

Materials and Methods
Line 150: Could you specify the height of the cores collected?

Results
Line 250: “whereas the concentrations of zeaxanthin were significant for both” is unclear to me? Do you mean both sampling campaigns and whole dataset?

Discussion
Line 310: Not sure that “certainly” is needed here
Lines 311-312: Could you provide any reference to support this statement?

Legends
Table 1
Change “,” for “;” after “(diatoms)”
Figure 1
Please italicize “Nitzschia pusilla”
Figure 3: All abbreviations in the RDA should be explained in the legend to make the reading of illustrations (tables and figures) easier.


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: TEMPORAL AND SPATIAL VARIABILITY OF TERRESTRIAL DIATOMS AT THE CATCHMENT SCALE: CONTROLS ON PRODUCTIVITY AND COMPARISON WITH OTHER SOIL ALGAE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Review on “Temporal and spatial variability of terrestrial diatoms at the catchment scale: controls on productivity and relation to other soil algae (#45133)” by Foets et al.

This paper present novel data on he structure and physiology of soil algae, specially focused on diatom ecology which is one of the fields of expertise of the authors. I have no serious objections against the publication of the paper. Hereby some comments that may aid the authors to improve the draft.
Experimental design: - I do not see the point of comparing biotic and abiotic variables measured simultaneously. I mean, the algal assemblage observed in soil samples has grown there for some weeks, and its characteristics (cell numbers, pigments…) reflect the environmental conditions during that period. However, only the data measured during sampling is taken into account. Since the authors have temporal data, maybe it is worth to use “time-weighted averages” or similar.
- Some data about the occurrence of dead, empty (allochtonous?) frustules would be useful.
- The reader is referred to a previous paper by the same authors with additional data on methods and sampling design. I’d appreciate rather to see all the data here, even if implies repetition of published info. I am particularly interested in the spatial arrangement of samples. In this regard, the statistical tests used depend strongly on whether the samples are independent or not. If the authors considered only a single “experimental unit” (the Attert River basin in Luxembourg) the samples can hardly be considered independent between them. This would require the use of “repeated measurements” tests rather than the ones actually employed. Spatial autocorrelation is neither considered. All this puts at risk the plausibility of the conclusions rendered.
- Specific concerns on statistics: Pearson’s test is used without previously testing its assumptions. It is said that correlated variables were removed prior to further analysis: both variables were removed?
- It is not stated whether if log transformation actually accomplished normalization. By the way, about data transformation: many biometricians rely on nonlinear transformations (logarithmic, square root, or reciprocal) because they jointly affect the linear predictor of the average as well as the distribution of the random component, and the joint effect may not always be that which is sought (Gregorie et al. 2008). Model parameters will lose their biological meaning along with distorting the functional relationship as a whole (Onofri et al. 2010). Thus, the transformed data do not necessarily bear any information of the original data, and the consequence of data transformation is not predictable in general (Norleans 2000). See also Games (1984).
- It should be highlighted somewhere (and not only in the figure) that residuals (unexplained) accounts for most (60%) of the variance in the dataset.
- A pity that the authors did not use their own cell measurements but that of Omnidia (averages). It has been reported that soil populations may have different morphometry than aquatic conspecifics.
- Kruskal-Wallis test assumes a similar shape in the distributions, except for a possible difference in the population medians. This is not demonstrated in the paper.
- Some name misspellings: pussila.
Validity of the findings: - The text is well documented and discussed, with updated references and, in general a good scientific style and English language.
- The approach followed by the authors is original and fills a gap in our knowledge of soil microbiology
- The conclusions are well supported by the findings reported. The figures and tables are OK

However, see above
Additional comments: Having all this into account, I cannot recommend the publication of the paper until all these issues are adequately corrected or discussed.

References

Games, P. A. (1984). Data transformations, power, and skew: A rebuttal to Levine and Dunlap.
Gregoire, T. G., Lin, Q. F., Boudreau, J., & Nelson, R. (2008). Regression estimation following the square-root transformation of the response. Forest Science, 54(6), 597-606.
Norleans, M. X. (2000). Statistical methods for clinical trials. CRC press.
Onofri A, Carbonell E.A, Piepho H.P, Mortimer A.M, Cousens R.D. 2010. Current statistical issues in Weed Research. Weed Res. 50: 5- 24. 4.


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: TEMPORAL AND SPATIAL VARIABILITY OF TERRESTRIAL DIATOMS AT THE CATCHMENT SCALE: CONTROLS ON PRODUCTIVITY AND COMPARISON WITH OTHER SOIL ALGAE
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I have some minor comments and suggestions for improvements of the manuscript:

i)	METHODS: It is not clear for me, why the authors log-transformed abiotic parameters except for pH prior to ordination analysis. I understand this approach in a biplot that shows the relationship between pH values and other type of data. However, to my knowledge, standardization (i.e., rescaling all the data of different range), not log-transformation, is usually performed prior multivariate analysis such as RDA.
ii)	RESULTS AND FIGURE 4: It would be helpful to know the results of the tests for variation partitioning approach. I would suggest adding the P-values of the tests to the results and to the Venn diagram.
iii)	DISCUSSION: I would  appreciate some discussion about the results of SEM chemical mapping.
iv)	INTRODUCTION AND/OR DISCUSSION: The authors mentioned three groups of algae present in temperate soils, cyanobacteria, green algae, and diatoms. Is it possible that Eustigmatophytes and Xanthophytes were also present in their samples? How common and abundant are these groups of Ochrophytes in temperate soils?
v)	DISCUSSION: The authors discussed the importance of cell size on chlorophyll concentrations between cyanobacteria and diatoms. How large are the cell size differences between green algae and diatoms?
vi)	REFERENCES: “Vincent, W.F., (2000)” has incorrect page numbers: 321-240.


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: TEMPORAL AND SPATIAL VARIABILITY OF TERRESTRIAL DIATOMS AT THE CATCHMENT SCALE: CONTROLS ON PRODUCTIVITY AND COMPARISON WITH OTHER SOIL ALGAE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have responded adequately to the questions raised. Hence, the paper has been substantially improved. I have now no objections to see this article published in PeerJ.
Experimental design: No comments
Validity of the findings: No comments
Additional comments: See above


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

Input:
Title: MUSCLE ACTIVATION VARIES BETWEEN HIGH-BAR AND LOW-BAR BACK SQUAT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is generally well written, however, there are times where the English language can be improved, via sentence re-wording. Specifically, lines 63-64, line 94 (I think you mean ‘performed’ not ‘designed’), line 186, and lines 209-211.

Please check line 65, and the associated reference. I believe that the LBBS is characterised by a decreased hip moment.

Line 211-214. I am not sure your statement here is completely correct. Glassbrook et al., (2019) did compare the HBBS and LBBS within a control group.

Lines 252-255. This is a very short paragraph with only two sentences. I suggest combining with another paragraph.

Although Rippetoe is a well-known name in strength training, is it possible to replace the reference on line 251 with an academic article rather than a book reference?
Experimental design: Please provide more detail regarding your subjects. You describe them as ‘experienced powerlifters’, and also ‘experienced in resistance training and performing squats’. Were they competitive powerlifters, or specifically training for powerlifting, or just general strength trained individuals? If competitive powerlifters, what level powerlifters were they, and are the 1RM numbers provided in line 86 from competition or training?

Line 96-97. Please provide a justification of why these percentages were chosen. I’m assuming it is so that both the HBBS and LBBS can be performed in the sessions without major fatigue, however, Glassbrook et al., (2019) showed it is possible to perform 1RM for both squat variations within the same testing session.

Line 108-110. Please update figure 1 to include a representation of all 19 markers, for example: doi: 10.1080/14763140903229476 or at least provide the anatomical locations of the markers in the model. At present figure 1 does not leave me confident that your methods are capable of measuring anterior pelvic tilt. It is not clear what pelvic locations are used to measure pelvic tilt. It is only once I search into the provided references, that I find other required markers for pelvic tilt measurement represented.

Was footwear standardised at all?
Validity of the findings: No Comment
Additional comments: No additional comments


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

Input:
Title: MUSCLE ACTIVATION VARIES BETWEEN HIGH-BAR AND LOW-BAR BACK SQUAT
Review round: 1
Reviewer: 2

Output:
Basic reporting: Figures 1 and 2 clearly illustrate the set up of the equipment and the differences in technique, which are very important to the reader. These are a great addition to the manuscript.
Line 27: Delete reference to body weight squats in the abstract
Line 44: This sentence should start, ‘The squat…’
Lines 44-48: Please add why the squat is so commonly used, based on the strong association between 1RM  performance and performance in athletic tasks and the fact that numerous researchers have reported increases in athletic performance with increases in relative squat strength.
Line 59: Delete the s off the end of ‘trainings’.
Line 62: Do you mean the lower part of the upper trapezius? Based on the trapezoid shape of the muscle the lower trapezius would be halfway down the individual’s spine.
Lines 68-70: Is the HBBS chosen due to the increased forward lean of the trunk in the LBBS?
Line 70: Please re-word this sentence, as studies are inanimate and therefore cannot analyse anything.
Experimental design: Why were loads associated with hypertrophy used, when the subjects were powerlifters and the maximal strength in this populations is explained as a key performance indicator within the introduction?
Why was EMG data not normalized to permit more effective comparisons between studies?
Effect sizes should be included within the statistical analyses to highlight if any observed differences were meaningful.
Lines 96-97: A strong and clear rationale for the use of these hypertrophy based loads is essential, especially in power lifters and when maximal performance in a back squat is associated with performance in athletic tasks.
Line 97-98: Please briefly describe the protocol.
Line 120: Figure 2 does not illustrate this, there are clear differences in depth and dorsi-flexion, which are likely to affect the resultant EMG due to differences in the length tension relationship.
Line 146: It is nice to see the 95%CI included, but the results should also be interpreted based on this, with associated thresholds highlighted here, please see: Koo and Li (2016). A Guideline of Selecting and Reporting Intraclass Correlation Coefficients for Reliability Research. Journal of chiropractic medicine 15(2): 155-163.
Lines 152: It would be useful to include effect sizes.
Results: Please make any amendments based on the interpretation of the ICC’s based on the lower bound 95%CI and the addition of the effect sizes and appropriate criteria for interpretation.
Validity of the findings: Why was EMG data not normalized to permit more effective comparisons between studies?
Line 146: It is nice to see the 95%CI included, but the results should also be interpreted based on this, with associated thresholds highlighted here, please see: Koo and Li (2016). A Guideline of Selecting and Reporting Intraclass Correlation Coefficients for Reliability Research. Journal of chiropractic medicine 15(2): 155-163.
Lines 152: It would be useful to include effect sizes.
Results: Please make any amendments based on the interpretation of the ICC’s based on the lower bound 95%CI and the addition of the effect sizes and appropriate criteria for interpretation.
Additional comments: This is an interesting and generally well written study, which will be of interest to practitioners, however, there are a few areas which require attention / justification:
Why were loads associated with hypertrophy used, when the subjects were powerlifters and the maximal strength in this populations is explained as a key performance indicator within the introduction?
Why was EMG data not normalized to permit more effective comparisons between studies?
Effect sizes should be included within the statistical analyses to highlight if any observed differences were meaningful.
In the Discussion, the differences in posture and therefore muscle lengths should be explored in relation to potential differences in EMG.
Figures 1 and 2 clearly illustrate the set up of the equipment and the differences in technique, which are very important to the reader. These are a great addition to the manuscript.


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

Input:
Title: MUSCLE ACTIVATION VARIES BETWEEN HIGH-BAR AND LOW-BAR BACK SQUAT
Review round: 2
Reviewer: 1

Output:
Basic reporting: "Comment 3. Line 211-214. I am not sure your statement here is completely correct. Glassbrook et al., (2019) did compare the HBBS and LBBS within a control group.
Answer 3. Indeed, Glassbrook et al., did compare the HBBS and LBBS within a control, inexperienced group but they only presented kinematic and kinetic data. The aim of our study was to compare muscle activities between HBBS and LBBS and Glassbrook et al., didn`t include EMG analysis in their research."

The sentence in the paper still doesn't reflect this. Glassbrook et al., and Wretenberg references appear before you even mention EMG. As it stands only Swinton is implied to not include EMG.

This sentence needs to be re-worded to clearly state your meaning/intention.
Experimental design: "Comment 7. Line 96-97. Please provide a justification of why these percentages were chosen. I’m assuming it is so that both the HBBS and LBBS can be performed in the sessions without major fatigue, however, Glassbrook et al., (2019) showed it is possible to perform 1RM for both squat variations within the same testing session.
Answer 7. These percentages were chosen due to the fact that some of the athletes were preparing for the National Academic Championships, so the load level was limited to 70% of 1RM in order not to interfere with individual training preparations (Issurin VB. 2010. New horizons for the methodology and physiology of training periodization. Sports Medicine 40:189–206 DOI: 10.2165/11319770-000000000-00000.) The load level limited to 70% of 1RM also let the athletes to perform their squats with the optimum and repeatable technique, which was designed to make the comparisons between both techniques more reliable.
Justification was added to the manuscript"

I can see that you have put this into a limiations paragraph, and have responded to a similiar comment from reviewer no.2. However, please add a similar (but shorter) statement in the methods section, which outlines why these percentages were chosen. A reader should be provided with this information earlier in the paper than the last paragraph of the discussion.
Validity of the findings: N/A
Additional comments: The authors have addressed the majority of my comments to a satisfactory level.
After addressing my remaining two comments, I am happy to recommend this study for publication.


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

Input:
Title: MUSCLE ACTIVATION VARIES BETWEEN HIGH-BAR AND LOW-BAR BACK SQUAT
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment, all previous comments have been addressed
Experimental design: No comment, all previous comments have been addressed
Validity of the findings: No comment, all previous comments have been addressed
Additional comments: No comment, all previous comments have been addressed


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

Input:
Title: MUSCLE ACTIVATION VARIES BETWEEN HIGH-BAR AND LOW-BAR BACK SQUAT
Review round: 3
Reviewer: 1

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: Authors have addressed my remaining 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: MULTIPLE IMMUNITY-RELATED GENES CONTROL SUSCEPTIBILITY OF ARABIDOPSIS THALIANA TO THE PARASITIC WEED PHELIPANCHE AEGYPTIACA
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. Goldwasser et al.2000 a and b is the same reference, similarly Tiryaki & Staswick 2002a and b;
2. I found it very difficult to read the graphs (Fig. 2- 4) and to draw a conclusion. It would easier if every pathway could be presented on a different graph or if not possible, maybe make it color coded to know in which pathways those mutants are involved; and make a line or cut off or mark somehow which mutants are less and which are more susceptible than WT.
3. Figure 5- there are some significance stars on the graphs but it is not mentioned in the legend or text how the statistic was done.
4. The time-lapse movie legend states that the experiment was done in Arabidopsis but for the above-ground growth tomato plants were used- this should be clarified in the movie description.
Experimental design: 1. Some of the mutants are wrongly described, for instance jar1 is involved in JA biosynthesis and not signaling
2. the qPCR data is not convincing and not really discussed in the manuscript however a big conclusion is drown in the abstract. It would be better to use several marker genes for each pathway. Also the way the statistical analysis was done is not indicated.
Line 273-276: "The largest magnitude changes in measured gene expression were upregulation in ethylene (ACS6), JA (VSP2), and Pattern- triggered immunity (PTI, WRKY53)".All these genes were not significant while the significant ones BOI and MYB51 are not discussed.
3. A very high concentration of GR24 (6,7uM) was used and still low germination of P. aegyptiaca seeds was observed. I find it a bit odd as I thought that these seeds are very responsive to strigolactones or maybe not the most appropriate germination stimulant was used?
Validity of the findings: Although the novel quantitative assay was developed to assess growth of Phelipanche aegyptiaca on the host A.thaliana, for me, on this stage the manuscript did not provide additional knowledge on which pathways are important for the parasite-host interaction. According to me, the authors are not very critical about their data and often make too strong and far-reaching conclusions. For instance, they claim that functional JA biosynthesis and signaling pathways are critical for full susceptibility to P. aegyptiaca parasitization, while only dde2, JA biosynthesis mutant is less susceptible not jar1 and not signaling mutants jaz3/jaz4-1/jaz9-1 or OE Jaz3 (T3), jin1-1 at early tubercle and  jaz3/jaz4-1/jaz9-1  mutant get less susceptible at late tubercle. I suggest to more carefully and criticaly reanalyze the data from mutants screen and to compare it with the qPCR results.
Also for pdf6 mutant, I agree that it is more susceptible than WT, but I would not make that strong conclusion that PFD6 is the immunity hub protein as its role in plant immunity was not studied in much detail.
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: MULTIPLE IMMUNITY-RELATED GENES CONTROL SUSCEPTIBILITY OF ARABIDOPSIS THALIANA TO THE PARASITIC WEED PHELIPANCHE AEGYPTIACA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The submitted manuscript by Clarke et al. with the title “Multiple immune pathways control susceptibility of Arabidopsis thaliana to the parasitic weed Phelipanche aegyptiaca” contributes new knowledge to the field of plant-parasite interaction. Phelipanche aegyptiaca, Egyptian broomrapes, is a parasitic plant that causes yield losses in tomatoes, carrots, and other crops (see Parker et al., 2012). Phelipanche infestations are notoriously difficult to manage, and genetic resistance is unknown.

Clarke et al. studied Arabidopsis thaliana as a host, rather than an economically important crop species. Working with the model species has the advantage of access to a large number of well-characterized mutants that can be shared between laboratories and tested with other parasites. Besides, working with Arabidopsis, a relatively small plant, is space-, time- and cost-effective. In line with previous studies, Clarke et al. show that at least early infection structures on Arabidopsis are comparable to other hosts (Westwood 2000, Bar-Nun et al.,2008).

The authors introduce in their manuscript a new quantitative assay for assessing the susceptibility of Arabidopsis towards P. aegyptiaca. The assay and the subsequent screening procedure of 46 Arabidopsis mutant lines are well-designed and well-documented. The authors provide sufficient background information, also, for readers of related research fields, e.g., plant immunity, plant hormone signaling. The manuscript is well structured, all figures, and movies, are relevant and of high quality. Raw data are accessible, as well as further in-depth documentation of the statistical analysis.
Experimental design: The authors discovered that Arabidopsis mutants with defects in the biosynthesis and the perception of the plant hormone jasmonate (JA) tend to support less P. aegyptiaca tubercle growth. In particular, the dde2-2 mutation negatively affected tubercle development in wild-type, sid2, and pad4 background, however not significantly in an ein3/sid2/pad4 genetic background. Similarly, the jar1 mutation that leads to reduced JA signaling in host plants negatively affect early and late tubercle development.

The other main discovery by Clarke et al. is that a mutation in the pfd6 Arabidopsis genes was linked to significantly more young tubercles, thus, indicating higher susceptibility. Pfd6 has not been studied previously in the context of parasitic plants. Pdf6 regulates immunity to bacterial pathogens through MTI, Microbe-associated molecular pattern-Triggered Immunity (Mukhtar et al., 2011). Clarke et al. study provide further evidence that parasitic plants trigger similar immune responses as microbial pathogens. An activation of MTI-like processes in Arabidopsis during Phelipanche infections was also seen in the up-regulation of the MTI-responsive gene WRKY53 in Figure 5.
Validity of the findings: In summary, the presented work by Clarke et al. is novel, exciting, and relevant, and I would like the authors only to consider the following minor points for revision:

Line 60: CuRe1 in tomato may be included as an example for a resistance gene detecting parasitic plants (Hegenauer et al., 2016) unless the authors refer to parasitic plants of the Orobanchaceae family only.

Line 109: Space missing in front of “mm”

Line 190: The authors wrote that their assay measures “attachment, vascularization, and tubercle growth.” The term “vascularization” is misleading here, as the assay did not assess the formation of vascular tissue, e.g., by stains or tracers per se, but uses tubercle growth as a proxy for successful vascular connections to host roots.

Figure 1B: “2 mg/ml” does not correspond to 6.7 µM GR24 (line 96).

Figure 1D: Please indicate on the x-axis or in figure legend if “% attachment” shows attachment relative to germinated seed or attachment relative to all seeds (germinated + un-germinated seeds).

Table S3: The aberrations “Quad sig” (likely) for dde2/pad4/sid2/ein2 is not explained in the text.
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: MULTIPLE IMMUNITY-RELATED GENES CONTROL SUSCEPTIBILITY OF ARABIDOPSIS THALIANA TO THE PARASITIC WEED PHELIPANCHE AEGYPTIACA
Review round: 2
Reviewer: 1

Output:
Basic reporting: This manuscript is now improved in response to the comments from both reviewers. It is clearly written and overstated conclusions were removed.
Experimental design: 1. I found one more mutant wrongly described in Table 1: sid2 is involved in SA biosynthesis not signaling.

2. I'm not sure whether paired t test can be used here for the qPCR data analysis as gene expression is compared between mock and treated plants and not twice for the same plant.

3. The concentration of GR24 was changed from 6,7uM to 2 mg/ml, which according to my calculation gives 6,7 mM so even higher than mentioned before. This should be clarified and maybe better to express it as molar concentration. Also the name "rac-GR24" instead of just "GR24" is now commonly used in the field.
Validity of the findings: All of my previous concerns were addressed.
Additional comments: The authors identified genes involved in resistance or susceptibility to P. aegyptiaca parasitization providing new knowledge to the field of plant-parasite interaction and giving a foundation for further studies.


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: MULTIPLE IMMUNITY-RELATED GENES CONTROL SUSCEPTIBILITY OF ARABIDOPSIS THALIANA TO THE PARASITIC WEED PHELIPANCHE AEGYPTIACA
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: The authors have satisfactorily addressed most of my questions. However, I am still confused about the actual concentration of GR24 that was used to pre-germinate P. aegyptiaca seeds. 2.2 mg/ml (~ 6.7 mM) would actually be three orders of magnitude higher than the previously stated 6.7 µM and also far above the range at which these germination inducers are applied in most studies. Maybe, there is only confusion about the final concentration in the Petri dishes, or perhaps this high concentration of GR24 was necessary to ensure homogenous germination. Either way, it is essential to clarify this point as it is a critical factor for any researcher who would like to conduct similar experiments.
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: A DE NOVO ASSEMBLY OF THE SWEET CHERRY (PRUNUS AVIUM CV. TIETON) GENOME USING LINKED-READ SEQUENCING TECHNOLOGY
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper reports the whole-genome sequence of sweet cherry, for which the authors used 10X Genomics Chromium technology.

Since the assembly presented in this paper is not dramatically improved in compare to the previous report, I recommend to delete "improves genome coverage and completeness" from the title.
Experimental design: The authors used 10X Genomics Chromium reads to estimate the size of the sweet cherry genome (299.17 Mb) and to evaluate the assembly qualith (99.02%). However, as the authors have already pointed out, it might be due to bias in the Chromium library missing 38 Mb. I strongly recommend the authors to analyze again with whole-genome shotgun reads obtained from a PCR-free method, e.g., TruSeq DNA PCR-Free Sample.
Validity of the findings: The text is totally descriptive and lacks any insights into biological aspects in sweet cherry.
Additional comments: Please consider the comments to improve this manuscript.