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: PATTERNS IN EVOLUTIONARY ORIGINS OF HEME, CHLOROPHYLL A AND ISOPENTENYL DIPHOSPHATE BIOSYNTHETIC PATHWAYS SUGGEST NON-PHOTOSYNTHETIC PERIODS PRIOR TO PLASTID REPLACEMENTS IN DINOFLAGELLATES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The literature on the topic is well cited. The figures effectively summarize the manuscript. Raw data are shared. The language is clear throughout most of the manuscript but there are parts where it needs to be improved. For a couple of sentences the grammar is clearly wrong.

This is largely an exploratory study, but it also serves to test one hypothesis, and provides a new hypothesis for one of the patterns found. Enough and sufficient backgrounds is provided for the reader to appreciate the relevance of the study and understand its contents.
Experimental design: This study presents original primary research that fits the aims and scopes of PeerJ. The research question is relevant and meaningful, but I wish the authors to better define it at the end of the introduction. As said before, this study is largely exploratory, but also tests a hypothesis. The methods are rigorous and appropriate to answer the research questions. The methods are mostly described with sufficient detail and information to replicate, but few comments on how to improve them can be found below.
Validity of the findings: The data are properly analyzed. The conclusions seem to follow the results logically. The hypotheses presented are interesting to stimulate further thought and can be linked to the patterns found.
Additional comments: In this manuscript, Matsuo and Inagaki investigate the phylogenetic provenance of the enzymes responsible for the biosynthesis of chlorophyll a, heme and isoprenoid precursors in dinoflagellates with derived non-canonical plastids (the fucoxanthin Karenia and Karlodinium, and the green Lepidodinium). Even though previous work had looked at the plastid proteomes in these species, no thorough attempt to compare all three pathways had been done before for all three species simultaneously. To achieve this, the authors provide a new full RNA-seq transcriptome, that of Lepidodinium, and perform phylogenetic analyses on each enzyme belonging to all three biosynthetic pathways. The goal of the authors is to find how chimeric the different plastid biosynthesis pathways in non-canonical dinoflagellate plastids are. In other words, are there patterns in the gene ancestry for these enzymes across the pathways in the different non-canonical plastids?

This is an interesting study. It is also well done. I think this study also helps to more systematically answer the question of what was the nature of the dinoflagellate hosts that acquired non-canonical plastids. It extends the hypothesis suggested for kareniaceans, i.e., that the host was heterotrophic with a relict plastid, to Lepidodinium. It seems to me that this is an interesting contribution because it suggests a convergent, and perhaps more generalizable, evolutionary route. It also implies that it is incorrect to call such examples ‘plastid replacements’ because both plastids co-existed at one point (and still might)—It was the acquisition of a new photosynthetic plastid alongside a no-longer photosynthetic relict plastid. This study also discovers interesting patterns of chimerism across these three biosynthetic pathways in plastids, and provides interesting hypotheses for the patterns observed, namely (1) none or few VI-type genes for the chlorophyll a biosynthesis pathway, and (2) few EA-type genes for all pathways in Lepidodinium.

I encourage publication of this manuscript in PeerJ. I do not have major objections to this study and its methods. My main comments concern the structuring of the manuscript.

My major comment is this:

-	Why do the authors want to investigate the gene ancestries of precisely these three pathways? If their ultimate goal is to better understand chimerism in these plastid proteomes, it would then be best to look at the whole proteomes, or at least more pathways (e.g., fatty acid biosynthesis, Fe-S cluster biogenesis, etc.). But if their ultimate goal is to test the hypothesis of whether the host that acquired these non-canonical plastids was heterotrophic, then the experimental design seems more suitable. It does make sense that by comparing the ancestry of the chlorophyll a biosynthesis pathway (which is dispensable depending on lifestyle) to those for heme and isoprenoid precursors (which became essential to cells) such hypothesis can first be tested. At least three alternatives can be discriminated: (A) the host was heterotrophic with no plastid at all (predicts mostly EA-type and LA-type genes for all pathways), (B) the host was heterotrophic but with a relict plastid (predicts VI-type for heme and isoprenoid biosynthesis, but EA- or LA-type genes for chlorophyll a biosynthesis), and (C) the host was photosynthetic (predicts a significant number of VI-type genes for all three pathways). Such predictions rely on the safe assumption that genes are lost easily if their functions are not required. Alternative C has been largely rejected by previous studies. Other studies have also provided support for alternative B over alternative A. One of the main contributions of this study is that it lends further support to alternative B. I think that the reasoning behind the experimental design of this study can be made more explicit in the introduction.

I now provide specific comments on each section:

Title

-	The title should be clearer and shorter. I think the major points made in the paper can be reflected in the title. For example: ‘Patterns in the origins of chlorophyll a, heme and isoprene biosynthesis pathways suggest a heterotrophic dinoflagellate host for non-canonical plastids.’ But other possibilities might be best.
- 	I also suggest using the word patterns rather than trends in the title and throughout the manuscript. A trend is a pattern throughout time. I think this study looks at patterns of gene ancestry among metabolic pathways.

Introduction

- 	I suggest removing the big section that describes the three pathways. They have been described elsewhere in the literature and make the introduction unnecessarily long. Fig. 1 is a good summary of such paragraphs. If desired, small molecule structures can be added to Fig. 1 to compensate for the lack of detail in the introduction after removing such paragraphs. This is all that is needed. I understand more background can help the non-expert, but a very long introduction and manuscript can also deter many other readers. We have all given up on manuscripts that become too long and tedious. One option is to move this text to the supplementary material. Mentioning the functionally equivalents (e.g., hemN and hemF, hemJ and hemY) of some of the enzymes can be kept in the introduction.
-	Some of this content in the introduction becomes redundant with further explanations in the Results section about what the enzymes do, for example.
-	Emphasize that you have sequenced a new transcriptome for Lepidodinium. This is valuable data.
-	I am glad that the authors have chosen the word ‘chimeric’ to refer to the patterns observed. There has been an unfortunate trend in the literature in referring to such patterns as ‘mosaicism’. Mosaicism well refers to a combination of ancestral and derived characters, and not to a combination of mixed ancestries.

Methods

-	Please make the alignments available online, especially because there were refined and trimmed manually which makes them less reproducible.
-	Transcriptomes tend to be comprised by incomplete transcripts. Most often they are incomplete at the 3' end. This is also the end which carries a splice leader (SL) in dinoflagellates. But looking for SLs can add further support to the idea that these are transcripts are genuinely dinoflagellate and not contaminants.
-	Please provide details about the sequencing of the Lepidodinium transcriptome, or cite a publication that does, and make it accessible to the scientific community.
-	How complete is the Lepidodinium transcriptome? A BUSCO analysis, for example, can give a hint.
-	Could there be LBA between some chlorarachniophyte and Lepidodinium genes? These could have been ‘green’ in origin, but similarly diverged considerably. Most sophisticated models could give clues, e.g., C10-60 models in IQ-TREE, or CAT-GTR in PhyloBayes.

Results

- 	The results section is organized around each biosynthesis pathway. This makes sense. However, the discussion provides too much detail. It can be summarized in some parts and refer to the Figs. 2-4 extensively. Please shorten. There appears to be some discussion in the results section too, e.g., 523-530.
- 	It is wise to withhold conclusions in the absence of statistical support for some of the trees, even though they might show some patterns in agreement with preconceived notions. I agree with the authors in their judgements.

Discussion

-	Statement in 783-784 does not seem accurate. Please revise.
-	Cavalier-Smith and Saldarriaga have also discussed such ideas (i.e., a hetrotrophic ancestor for non-canonical plastids in dinoflagellates) in their papers before. I suggest they are cited and discussed.
-	The hypothesis put forward to explain why EA-type proteins are not common in these pathways in Lepidodinium makes sense. But the data are too limited. Looking at the whole proteome can more thoroughly test such an idea.

Figures

-	The figures are well made and quite effectively summarize the manuscript. For example, Fig. 1 summarizes the biosynthetic pathways, Fig. 2-4 present simplified trees for all enzymes of the pathways under study, and Fig. 5 synthesizes the main findings in regard to the phylogenetic ancestries of each enzyme.


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: PATTERNS IN EVOLUTIONARY ORIGINS OF HEME, CHLOROPHYLL A AND ISOPENTENYL DIPHOSPHATE BIOSYNTHETIC PATHWAYS SUGGEST NON-PHOTOSYNTHETIC PERIODS PRIOR TO PLASTID REPLACEMENTS IN DINOFLAGELLATES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors should ensure that all alignments and tree outputs generated in this study are publically accessible, either as supporting data here, or on an online repository, such as Treebase.
Experimental design: 1) The absence of UROS/ CPOX from Karenia and Karlodinium respectively is puzzling, and I am not confident that this reflects, as stated, absence from the MMETSP transcriptome libraries. These libraries are massive- by my count about 72000 non-redundant transcript sequences in the Karlodinium combined assemblies, and over 400000 between all four Karenia combined assemblies, and in each case there are four independent replicates of each transcriptome library- I fail to see how a fundamental component of tetrapyrrole synthesis would not be detected in these libraries, particularly if all other components are. Other possibilities that should/ could be considered:

- Is there any evidence for UROS transcripts in the unassembled reads (as opposed to assembled transcripts) from Karenia, or likewise for CPOX in Karlodinium?
- Are there alternative pathways that might function to convert hydroxymethylbillane into protoporphyin IX in either species? How many different isoforms of each sequence did the authors use as search queries? Might (for example) a mitochondria-targeted protein, or query from a plastid-lacking species, give different results than a query of plastid/ cyanobacterial origin?
- Is there any possibility that either UROS or CPOX has become fused to another protein in the tetrapyrrole biosynthesis pathway in either species- e.g. is there a UROS domain on Karlodinium HMBS or similar?

2) The only other major concern I have is of contamination in some of the transcriptome libraries considered, which may either result from non-axenic cultures or (in the case of MMETSP) technical contamination resulting from pooling libraries from different species in the same sequencing reaction. Ideally the authors should use decontaminated versions of the Karenia and Karlodinium reference libraries (c.f. Marron et al., 2016; Dorrell, Gile et al., 2017) to avoid mis-identifying sequences of non-dinoflagellate origin as being present in each species.

Furthermore, the authors should provide evidence that any transcripts with atypical evolutionary inheritance patterns (and particularly transcripts for which two orthologues of separate evolutionary origin, c.f. the prokaryotic red UROS, and GTR, are detected), are indeed genuine components of the transcriptomes in question: this could be a matter of identifying the same transcript repeatedly in multiple libraries from the same species, or for example looking at the nucleotide composition and/ or codon usage patterns associated with the atypically inherited transcripts. The phylogenies here do not need to be redone, but the authors should be prepared to justify that isolated and/ or atypically inherited transcripts identified in each species are genuine.
Validity of the findings: Some of the evolutionary assignations made by the authors are questionable. For example, lines 352-353 state  "The second Karlodinium [UROS] sequence… tied with the sequence of a red alga Rhodosorus marinus … suggesting that the Karlodinium-2 sequence was acquired from a red alga". Consulting the tree topology shown in fig. S1, I see no convincing evidence for a red-to-Karlodinium transfer: rather the Karlodinium/ Rhodosorus clade form an isolated group within a clade of otherwise prokaryotic sequences, and indeed all other red algal sequences in the tree (including one other isoform from Rhodosorus). It is equally possible in this case that the Karlodinium sequence was acquired from a bacterium, then transferred to Rhodosorus; that both lineages acquired orthologous sequences from related bacteria; or that either of both sequences are the result of prokaryotic contamination in the Rhodosorus/ Karlodinium sequence libraries (see above).

As a general rule of thumb, I would only recommend assigning specific evolutionary origins if the Karenia/ Karlodinium sequences resolve within a paraphyletic group of organisms with a common evolutionary origin, or at the very least that there are a minimum of two or three sequences with the sister-group affiliation in the tree. This may reduce the number of (particularly LA-) inferences made in the manuscript, but I would rather the authors present a smaller number of more credible relationships, than try to report everything that may or may not be present.
Additional comments: General manuscript point: full species names need to be supplied throughout- there are more than one Karenia (brevis, mikimotoi), Karlodinium (veneficum/ micrum, armiger) and Lepidodinium species (chlorophorum, viride) that exist!

Line 59: should be "the vast majority"

Line 78-83: it would be good to mention recent work (c.f. Matsuda et al., 2017, Zerdoner Calasan et al. 2017) indicating that dinotom endosymbionts are evolutionarily transient, potentially subject to frequent replacement, and therefore a direct comparison between them and more evolutionarily permanent plastid lineages is inappropriate

Line 84: should be "as prey". Could you give some examples of key genera, and the types of algae they ingest?

Lines 89-96: I would like to see a slightly more extensive discussion of what is already known about host-derived contributions to fucoxanthin and Lepidodinium plastid proteomes- as it is greater than is suggested by the authors. In particular, they should acknowledge (either here, or in the Discussion, lines 807-809; 846-849):

- There are actually quite a lot of examples known of proteins, targeted to serially acquired dinoflagellate plastids, of peridinin origin- alongside Minge 2010 and Bentlage 2016, the authors could/ should cite Patron 2006; Nosenko 2006; or Dorrell and Howe 2015 (as a summary of everything that has previously been identified to be of peridinin origin in each lineage)

- Among the proteins identified to be of peridinin origin are subunits of the photosynthetic electron transport machinery (e.g. atpC in Karlodinium; Patron et al., 2006; and FNR in Lepidodinium, Minge et al., 2010). This argues against (lines 807-809. 846-849) the common ancestors of the fucoxanthin and Lepidodinium lineages being obligately non-photosynthetic, or at the very least implies that whatever loss of photosynthesis occurred was relatively transient, and did not lead to the loss of all photosystem-associated genes of peridinin origin from the host genome.

- Similarly, the presence of RNA modification pathways derived from the ancestral peridinin plastid in the fucoxanthin plastid lineage (c.f. Dorrell and Howe, 2012; Jackson et al., 2013; Richardson et al., 2014), might be consistent with the ancestor of the fucoxanthin lineage retaining some form of plastid genome, even if this genome was associated with a leucoplast or vestigial plastid, from the peridinin lineage, until shortly before the acquisition of the replacement. The authors could also note that peridinin-type RNA modificiation pathways do not function in Lepidodinium (Richardson et al., 2014), which mirrors the lower incidence of EA-derived proteins in heme and IPP synthesis.

Line 102: should be "a sppA gene, encoding serine proteease IV, of green algal origin was detected in Karenia…and a csp41 gene, encoding an mRNA-binding protein, of putative stramenopile origin was detected in Lepidodinium". How robust is the support for these relationships?

Line 108: should be "varies"

Line 109-111: "Likewise, we are uncertain…plastid" doesn't make sense. Perhaps the authors mean "we are uncertain whether there is an evolutionary consistent trend in chimerism"- please check and verify

Line 126: should be "We are aware"

Line 132: should be "is catalysed"

Line 148: should be "use the pathway"

Line 149-151: rephrase. Typically the past tense is only used when referring to a specific study or time point (e.g. "In a recent study by Koreny et al., 2013, neither X nor Y were detected")- otherwise this should be in the present tense (e.g. "Neither X nor Y appear to be present")

Lines 152-154: more strictly chlorophyll and heme share a common precusor biosynthesis pathway, which branches based on the chelation of either Mg/ Fe and the downstream processing steps that occur

Line 159-166; lines 580-582: to my knowledge MgPME cyclase has never been detected in eukaryotes outside of the land plants (c.f. Wilhelm et al., 2006; Nymark et al., 2009), and ycf59 (the inferred membrane-bound subunit of MgPME cyclase cf. Peter et al., 2011) typically has a restricted, plastid-encoded distribution outside of the green lineage. So I would be cautious in general about emphasing the presence, origin, or functional importance of MgPME cyclase, at least until we have a better idea of the diversity of chl branch synthesis pathways in non-green plastids.

Lines 239-241: did the authors look at the individual transcriptome libraries, or combined assemblies, generated for Karenia and Karlodinium? This is particularly important in the context of contamination (contaminant sequences may not be present in all libraries from one species), but in either case the specific version and accession date of the transcriptome libraries should be provided.

Lines 242-243: the final set of query sequences used for this study should be presented as a supporting dataset

Line 301-302: to my knowledge, SignalP 4.1 does not allow the prediction of TP-like regions- do the authors mean TargetP1.1 (for example), applied to a truncated sequence following prediction of an SP by SignalP4.1? If so, clarify. It would also be good to briefly profile the length and net charge associated with the predicted TP regions in each sequence, given that previously characterised nucleus-encoded and plastid-targeted proteins in fucoxanthin-containing dinoflagellates are demarcated by having a relaxed charge balance (Patron and Waller, 2007) and longer TP region (Yokoyama et al., 2011) than equivalent BTSs from haptophytes.

Line 336-337, and elsewhere: if the BLAST analyses were performed using the individual libraries (rather than pooled assemblies) from Karenia and Karlodinium, it is possible that monophyletic groups of sequences from one species might in fact be different assemblies/ annotations of the same transcript from different libraries, as opposed to different transcripts from paralogous genes. At least one of the Karlodinium PGBD sequences, for example, is on a very long branch, which could be consistent with a partial/ incomplete copy of the same gene, as opposed to divergent paralogues, from different transcriptome libraries. Alignments in these cases would be useful, particularly to identify base polymorphisms or other features that distinguish different transcripts from the same species, and are unlikely to be the result of assembly.

Line 392: should be "a single version was identified in Karlodinium"

Lines 423-425: "pioneering studies have documented such evolutionarily chimeric plastid proteomes in dinoflagellates bearing non-canonical plastids, but primarily emphasized the presence of EA-type proteins to demonstrate the integration of a haptophyte endosymbiont into the dinoflagellate cell as the plastid." - citations needed here.

Line 553: chlI has in fact been detected in plastid transcriptome data from Karenia mikimotoi (Dorrell et al., 2016). It would be useful to inspect this sequence for the presence of a 3' poly(U) tail, which is characteristic of dinoflagellate plastid-derived transcripts in MMETSP data (Dorrell, Klinger et al., 2017)

Lines 600-601: technically it is possible that there is a light-independent POR in the Karlodinium plastid genome as the published genome sequence is incomplete, although no such transcripts are detected in Karenia mikimotoi plastid transcriptome data (as above)

Line 796: should be "in heme biosynthesis"

Line 806: should be "notably"

Lines 832-834: the authors could mention here that Karenia and Karlodinium appear to be quite distantly related to one another (Bergholtz et al., 2006), and indeed their plastid genomes have different associated gene contents (Gabrielsen et al., 2011; Dorrell et al., 2016), which would be consistent with their assertion of divergent evolution in plastid proteome content between the two genera.

Lines 857-876:  The authors discuss possible factors underpinning the presence of laterally acquired proteins, such as the presence of chlorarachniophyte-derived proteins in the chl biosynthesis branch of Lepidodinium. While this discussion is detailed, I think that it misses the possibility that the LA-derived proteins might have originated from an endosymbiont that was already chimeric in nature, prior to uptake.  This is particularly likely for the fucoxanthin plastid, as its ancestor occupies a very deep position on the haptophyte tree; as a sister-group to the prymnesiophytes, and we have no real idea what suite of plastid-targeted proteins it possessed prior to uptake. Likewise it would be interesting to consider whether there may have been horizontal gene transfer from chlorarachniophytes into the pedinophyte ancestor of the Lepidodinium plastid, particularly given the presence of an endosymbiont-derived POR in the Lepidodinium transcriptome.

Line 909: should be "much more substantially"


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: PATTERNS IN EVOLUTIONARY ORIGINS OF HEME, CHLOROPHYLL A AND ISOPENTENYL DIPHOSPHATE BIOSYNTHETIC PATHWAYS SUGGEST NON-PHOTOSYNTHETIC PERIODS PRIOR TO PLASTID REPLACEMENTS IN DINOFLAGELLATES
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is in most cases clearly written and in general easy to read. However there are a number of small mistakes throughout the manuscript (wrong usage of tenses and several words, is/are or was/were mistakes, missing “the”s and some grammatical issues) as well as several sentences that need rewriting (e.g. page 11, lines 5-8; page 11, lines 20-23; page 17, line 5-7; page 27, lines 13-15; page 41, lines 20-23). Therefore I suggest that the authors ask a proficient English speaker to go through the manuscript and correct those small mistakes, which would improve readability and make for an easier understanding of the article.

The authors include literature references throughout the article and seem to be up-to-date within the field (except for a couple issues I am going to mention below in “Validity of the findings”). There are a few statements where references should be added:
Page 6, lines 19-23:
The three pathways in photosynthetic eukaryotes and those in cyanobacteria are principally homologous to each other, suggesting that the pathways in photosynthetic eukaryotes can be traced back to those endosymbiotically acquired from the cyanobacterial endosymbiont that gave rise to the first plastid (primary plastid).
Page 8, lines 2-6:
Overall, land plants used the pathway of cyanobacterial origin with modifications described below. (i) PBGD, UROS, and UROD, which are likely acquired from phylogenetically diverse organisms in non-endosymbiotic contexts, were identified. (ii) Neither hemN-version of CPOX nor hemJ-version of PPOX was detected.

The authors provide sufficient background information for their research and one might argue – and this is a minor quibble - it is almost a bit too detailed. All three pathways discussed are well described in the literature and while it is understandable that the authors want the information for the reader to be readily available, the pathway description is already extremely detailed in the Introduction and then the function of the single enzymes is described again in the Results. Altogether this makes for a very long read and I think the article would benefit from making at least the Results section a bit more concise (i.e. not repeat parts from the Introduction to such an extent). A good example is the subchapter “Genetic influx from phylogenetically diverse organisms shaped the Lepidodinium pathway”, which is more concisely written than the rest and still clearly conveys the results.
Experimental design: The authors state that their goal is a systematic evaluation of the impact of “exogenous” genes on several metabolic pathways situated in non-canonical plastids of dinoflagellates. Such a systematic analysis and comparison between non-canonical dinoflagellate plastids of different origins has not been undertaken before and provides valuable insight into the evolution of such plastids.
The tree reconstructions were performed with two different methods, with the maximum likelihood trees having been calculated with the best fitting model for each individual alignment and the Bayesian analyses being based on four independent chains, indicating a careful and concise methodological approach by the authors.
Minor comments:
- it would be helpful for readers to add a list of all taxa used in the analysis as Supp. Table
- what do the dashed branches in the tree figures represent?
- the algorithm(s) used with MAFFT should be indicated
- define KOIDs
- indicate which KOIDs belong to which pathway
- it is not clear which sequences from the KEGG database were used as queries in the initial BLAST - all of them? (see page 12, lines 8-9)
Validity of the findings: Overall the findings are represented in a clear and valid manner, however I do not agree with several concluding statements which I will detail below:

A. Several times in the Results section the authors claim a phylogenetic association that is not very well supported by the trees in question. In general, those are phylogenies where the query sequence clusters with only one sequence from another eukaryotic group and in one case this group is only represented by this one sequence in the tree. Examples are:

- in the UROS tree (Karlodinium-2 clusters with a single red algal sequence; page 17, lines 8-11)
- in the UROD tree (Karenia-3 clusters with the only euglenozoan representative in the tree; page 18, lines 1-3)
- in the ispD tree (Lepidodinium-1 clusters with a single stramenopile sequence in the absence of a monophyletic, well-supported stramenopile clade; page 33, lines 5-8)

I think in those cases the authors should make more careful statements and include other possibilities leading to such topologies, such as low taxon sampling (euglenozoa), relatively short sequences (single gene trees) and contaminations (MMETSP data are known to be contaminated), into their conclusions.
Additionally, the statement on page 34, lines 23-25 is not supported by the tree – the topology placing the apicomplexans/chromerids within the dinoflagellates is not supported and the authors state themselves that the removal of the rapidly evolving apicomplexan/chromerid sequences strongly improves the support of the clade. It should be re-formulated as well.

B. The authors base some of their conclusions (see also point C below) on the wrong assumption that Karenia and Karlodinium share the same endosymbiont, i.e. the ancestor of both has already acquired the endosymbiont. While it cannot be excluded that the ancestor already had a symbiont before the divergence, the current haptophyte plastids in those two lineages come from two different sources as shown by Gast et al., 2007 (doi:10.1111/j.1462-2920.2006.01109.x) in a 16S phylogeny. Therefore, the authors should rephrase the fragment on page 29, lines 8-9

“which were acquired from the haptophyte endosymbiont resided in the ancestral kareniacean species”

and reformulate the statement in their Discussion on page 38, lines 14-16:

“These observations suggest that the reconstruction of metabolic pathways in the haptophyte derived plastids (i.e. gene acquisitions/losses) was not completed before the separation of the genera Karenia and Karlodinium.”

C. A minor issue but although there is no Karenia plastid genome, there is a Karenia transcriptome available, created by Dorrell et al., 2016 (https://doi.org/10.1007/s11103-015-0408-9), that allows comparison of the gene content of both plastids (which the authors of that publication do). According to that publication, Karenia plastids encode ChlI, like the Karlodinium plastid, but their overall gene content is not the same, so the authors should rephrase the following statements and update their references:

Page 26, lines 3-7:
“Although no plastid genome data is available for Karenia, we identified the ChlI sequence in the transcriptomic data of this species (contig No., 0173787962). According to the intimate organismal relationship between Karlodinium and Karenia, we considered that the Karenia ChlI sequence was transcribed from the plastid genome.”

Page 28, lines 8-10:
“No gene for light-independent POR was found in the plastid genome of Karlodinium (Gabrielsen et al. 2011), implying that kareniacean species lack the light-independent version.”

D. A very minor issue, but the authors should mention the difference in results between their GSAT analysis and the phylogeny recovered by Cihlář & Füssy et al, 2016, as they specifically discuss Karenia in that context.
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: PATTERNS IN EVOLUTIONARY ORIGINS OF HEME, CHLOROPHYLL A AND ISOPENTENYL DIPHOSPHATE BIOSYNTHETIC PATHWAYS SUGGEST NON-PHOTOSYNTHETIC PERIODS PRIOR TO PLASTID REPLACEMENTS IN DINOFLAGELLATES
Review round: 1
Reviewer: 4

Output:
Basic reporting: The article is written in professional English, however, it countains several grammatic and stylistic mistakes, a few sentences are missing words (e.g., lines 83, 126, 253, 326) and would benefit from proof reading by a native speaker. The wording is sometimes a bit clumsy, but the text is unabiguous and clearly understandable. There are a few typographical mistakes such as combining "twenty two" and "27" in the same sentence (line 543).
The literature is properly referenced and the sources are relevant and numerous.
The introduction provides good context and successfully explains the relevance of the study and that the evolutionary story it wants to deliver is interesting. The authors manage to clearly describe the aims of the study including a good clarifying disclaimers on which topics will not be addressed and why. The Introduction chapter contains quite detailed description of the metabolic pathways and their particular steps which I find a bit unnecesarilly extensive and detailed since the paper is of evolutionary biology, not biochemistry. The text on lines 211-225 should be a part of Results or shortened significanlty to form a brief conclusion for the Introduction and outset for the next chapters describing the results.
The title of the paper is descriptive and clear, I would however suggest a shorter title and omit the unnecessary buzzword ("Trends in X").
I see a problem with structuring of the whole article. First, the distincion between "Results" and "Discussion" sections is not fully respected: the paper reads kind of like it was originally written in a format that merges "Results and Discussion" into one chapter. The "Results" section contains many interpretations of the presented data and speculations made based on them (e.g., lines 369, 387, 408, 411, 490, 507, 523, 542, 572, 623, 756 and many more), which I believe should be a part of "Discussion". The chapter is also very long and sometimes exhausting to read: ommiting the interpretative parts and structuring the text into smaller subchapters (I would suggest a subsection for each gene, and would prefer the Kareniacean and Lepidodinium phylogenetic data to be adressed together as they are based on the same trees anyway.) The "Discussion", on the other hand, is quite brief, albeit poignant and telling an interesting story. I have several suggestions for additional questions to discuss (see the end of the “Validity of findings“ section).
The text contains quite a lot of abbreviations. They are in most cases clearly explained at their first occurence, but nevertheless, I would find the inclusion of an index of used abbreviations useful.
The article includes five color figures which are well labeled and of good esthetic quality.
Figures 2-4 are nice and clear and elegant to look at but would lose informativity if printed by black and white printer or read by a person with some degree of colorblindness (around 7 % of males). I would strongly suggest adding another distinction between the colored taxons (symbols, abbreviations or line type). Moreover, the color distinctions are described in the text and might be a bit confusing since the verbal description of the colors might differ subjectively and between readers from different language/cultural backgrounds - the legends included directly in the figures would solve this issue. On the other hand, figure 5 would benefit from color distinction between the four categories (for example red, i.e. same as in the trees, for VI, brown/orange for haptophyte EA and green for chlorophyte EA, another color for LA, and grey for unknown), the differencies in the ratio of these categories in the two groups of organism would be more visible.
A few requests for clarifications:
- On line 82, authors suggest that the interlock between host and endosymbiont naturally lead to their genetic connection. This doesn't need to be the case since there are endosymbioses known to exist for hundreds of millions of years without its members merging into a genetic chimera.
- On line 118, the authors state that the [metabolic pathays] are "nucleus-encoded" but do not clarify which organisms/taxons are they refering to.
- On line 600, the authors state that no light-independent POR was found in the previous analysis of Karlodinium transcriptome. Does this mean they also searched for it in their data and failed?
Experimental design: I find the experimetal design to be appropriate to the aims of the study.
The investigation was performed to appropriate methodological and technical standards

The supplemental data contain full trees but not the alignments used for their construction which unfortunately makes the results non-reproducible, especially since the editing/trimming of the alignments was done manually. Please, include the alignments and ideally a file with the exact parameters of the RAxML analysis.
Some informations are present in the supplemental files, but they are not references in the text (the method for transit peptide prediction, substitution models selected by ProtTest...).
Validity of the findings: The study presents novel findings on the evolutionary stories behind a wide set of plastid metabolism-related genes in three species of dinoflagellates with non-peridinin plastids, many of which were first identified in the sequence data in terms of this study.
Data is robust and statistically sound as much as an evolutionary study can be. The phylogenetic analyses were done responsibly and the interpretations of the tree topologies is appropriate: the authors infer evolutionary scenarios based on the high-supported data only, and treat the low-supported results with corresponding caution.
The authors use the profile of gene origins (vertical inheritance, endosymbiotic transfer or lateral transfer) to reconstruct the evolutionary history which led to the establishment of the extant plastids in Karenia, Karlodinium and Lepidodinium which replaced the ancestral peridinin-containing plastids. The Discussion addressing these scenarios is performed with caution, yet it still postulates several intriguing stories and bright, out-of-the-box ideas.
Here are a few suggestions/questions to include in the Discussion to make it more rich:
- The authors decided to classify the gene origins as "vertical", "endosymbiotic" and "lateral". The "lateral" category includes both plastid-containing organism and organisms without plastids. What is the author's reasoning behind not separating these two subcategories?
- The authors keep refering to dinoflagellate genes related to/nested inside chlorarachniophytes as "acquired from chlorarachniophytes". Is there any taxonomical or evolutionary datation evidence for this claim? As far as I know there is no datation available for any of the endosymbiotic events in question - so the direction of the transfer cannot be inferred with certainty.
- How would the relationship between the dinoflagellate and the chlorarachniophyte donor of plastid-related genes look like? Are there any hints in the ecology of the extant species? Where do organisms of these taxons live, do their geograophical/ecological niches overlap? What would drive the frequent shifts between predation and phototrophy?
- Is it possible that the peridinin-containing plastid and the haptophyte-related plastid coexisted for a certain period of time in the dinoflagellate cell? How would this reflect on the gene phylogenies?
- Do I understand it correctly that the authors postulate two cycles of plastid photosynthesis loss and subsequent establishment of a new, unrelated one, for the evolutionary history of Lepidodinium on lines 846-849? Does this scenario makes sense in regard to the datation / the millions of years needed to go throught such changes? Any estimate on how old the plastids are? Where would the selective pressure to switch so frequently between non-photosynthetic plastid / predation / phototrophy come from? Which enviromental or ecological changes would cause such frequent shifts in the selective pressure in one lineage?
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: PATTERNS IN EVOLUTIONARY ORIGINS OF HEME, CHLOROPHYLL A AND ISOPENTENYL DIPHOSPHATE BIOSYNTHETIC PATHWAYS SUGGEST NON-PHOTOSYNTHETIC PERIODS PRIOR TO PLASTID REPLACEMENTS IN DINOFLAGELLATES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Line 90: should be “are composed of proteins with diverse evolutionary origins”
Line 110: should the “their cyanobacteria ancestry”
Line 129: should be “neither of the enzymes…has been detected in complex algae”
Line 306: should be “hydroxymethylbillane”
Line 425: should be “the donor of the GTR gene to L. chlorophorum remains unclear”
Line 502: should be “in heme biosynthesis”
Line 505: should be “is most prominent”
Lines 705-706: should be “two scenarios remains possible” and “originated from a stramenopile”
Line 723-724: should be “recovered a monophyletic clade containing the two…”
Experimental design: For lines 532-534: it would take all of about 3 days to verify the presence of a poly(U) tail on the K. brevis chlI by RT-PCR with an oligo-d(A) primer, if the authors had RNA/ cDNA/ time remaining to do this. I stress this is completely optional, but it would be fast and easy to perform.
Validity of the findings: thank the authors for exercising caution in defining the phylogenetic origins of LA-type genes with uncertain topology. I stress that this was requested not due to discomfort over the idea of LA-type genes, which is a really nice idea. I made these requests purely to maximise the subsequent impact and credibility of this study, i.e. to avoid giving ammunition to peer researchers sceptical of HGT through the over-interpretation of ambiguous tree topologies. By minimising this the authors also draw attention to very well-resolved examples of LA genes in their data, e.g. the green algal ChlH genes in Kareniaceae.

The only remaining statements where I could, in theory, drive a nail would be-

 Lines 473-474: it isn’t clear directly from Fig. 2G that the Lepidodinium-2 and -3 CPOX sequences are specifically of diatom origin, rather they form a sister-group to a clade of diatoms, with Chromera as a sister-group, followed by Chattonella as an outgroup. The authors don’t need to revise the figure in any way, but I would recommend downgrading these enzymes to being “of stramenopile origin” or “ochrophyte origin” for posterity. Conversely the Lepidodinium ChlD could be upgraded to being specifically of diatom origin based on the clade composition (lines 645-646).

Lines 579-580: the bootstrap support for all of the sub-clades within the haptophyte/ stramenopile clade are too weak to be certain of an LA v EA origin. I would suggest either dropping this statement or provide the alternative that this could be an EA gene with a poorly composed clade. Alternatively, if sister-group identity (rather than bootstrap resolution) were taken as adequate for defining evolutionary origin, then presumably the Clade 1 POR in both Kareniaceae (lines 594-595) should presumably be EA rather than ambiguous EA/LA.

Lines 705-706: presumably then Ochromonas could also have picked up an IspD gene from Lepidodinium. Perhaps it would be better to say that “the IspD sequence was transferred between Lepidodinium and Ochromonas”, which makes no assertion of direction.

Lines 847-849: while the Gast et al. study does show a distinct origin for Karenia and Karlodinium, the bootstrap support is non-existent, and a lot of prior and subsequent multigene studies (c.f. Takishita et al. 1999, 2000, 2005; Gabrielsen et al. 2011, Dorrell and Howe 2012) resolve monophyly for the fucoxanthin lineage. I would recommend not discussing this point. I do agree that getting more haptophyte sampling depth would be ideal to resolve the precise evolutionary histories of the LA proteins identified in this study.
Additional comments: I am largely happy with the revisions made to this manuscript. Provided the attached revisions are made, I feel it is ready 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: PATTERNS IN EVOLUTIONARY ORIGINS OF HEME, CHLOROPHYLL A AND ISOPENTENYL DIPHOSPHATE BIOSYNTHETIC PATHWAYS SUGGEST NON-PHOTOSYNTHETIC PERIODS PRIOR TO PLASTID REPLACEMENTS IN DINOFLAGELLATES
Review round: 2
Reviewer: 2

Output:
Basic reporting: The article is written in a clear, professional English, although it is still not perfect from the stylistic and grammatical standpoint. The sources are properly referenced and up to date, with a number of them being added recently to the paper's advantage. The introduction has been significantly shortened and made more poignant and easier to read, it communicates the context and aims of the study well and provides clear outline of what the authors want (and do not want) to address and investigate and why. The study discusses an impressive number of separate phylogenetic analyses which makes the resulting descriptions of results and discussion quite long and exhausive, and makes it hard and even contra-productive to try to clearly separate "results" from "discussion". The authors, nevertheless, did their best to present their findings in an organized and pregnant way. The text is now a bit briefer and no longer contains redundant passages. The requests for clarification or re-wording I posed previosuly were answered to my satisfaction.
Experimental design: The experimetal design is appropriate to the aims of the study which are clearly described and substanciated. The investigation was performed to appropriate methodological standard and the authors generated great amount of data and phylogenetic analyses. The requests for alignments and elaboration on some of the methodic approaches were answered and the information in question is available in either supplemental data or the text itself.
Validity of the findings: The study presents an evolutionary story behind a relatively wide set of plastid metabolism-related genes in three species of dinoflagellates whose ancestral peridinin plastids were lost ad replaced in the course of evolution. The set of genes/metabolic pathways was selected quite arbitrarily - as a model to investigate more genral trends in the dinoflagellate plastid evolution, this approach is made clear by the authors and justified. In fact, the volume of analyzed data (the number of observed genes times the number of organisms with different plastid evolutionary history) is very impressive, especially considering this is a study by two authors. Many of the genes were first identified or first sequenced in terms of this study.

Data is robust and statistically sound as much as an evolutionary study can be. The phylogenetic analyses were done responsibly - the authors used two independent methods and each alignment was assigned the corresponding substitution model individually. All the used data was also thoroughly screened for possible contaminations. The interpretations of the tree topologies were done with corresponding caution, yet they still postulate several interesting stories and clever, out-of-the-box ideas.

Most of the suggestions for the discussion enrichment I posed previously were not included in the manuscript, but I appreciate the authors effort to keep the text shorter and "down to Earth",i.e. devoid of too much of a theorizing.
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: PHYTOCHEMICAL COMPOSITION AND IN VITRO ANTIOXIDANT ACTIVITIES OF CITRUS SINENSIS PEEL EXTRACTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: Material and Methods

1.	I believe as the peels were collected from an orange juice manufacturer the waste is composed by the flavedo and albedo. I encourage the authors to clarify it in the M&M section.

2.	How long the drying process took? I also encourage the authors to add the information about the drying time and size of particles.

3.	Why choose water extraction process that use boil temperature since higher temperature for a long time may “destroy” phenolic compounds?
Validity of the findings: Conclusion

4. First paragraph of the conclusion seems to fit in the results section. Conclusion should relate directly to the questions brought up in the introduction. The second paragraph is a good example of it.
Additional comments: The current manuscript has significant information for the scientific society. Fruits and vegetable waste management is a challenge and also represent a company cost. Reduction, reuse and other strategies can be applied. Also, these wastes are rich in antioxidant components which can be used in the food industry.  All the assays are appropriate for the proposal of the study. The manuscript requires a few adjustments to be more informative to reader before acceptance.


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: PHYTOCHEMICAL COMPOSITION AND IN VITRO ANTIOXIDANT ACTIVITIES OF CITRUS SINENSIS PEEL EXTRACTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general, the manuscript is written clearly and based on recent citations.

Considering that one of the objectives of the study was to analyze the phytochemical composition and antioxidant capacity of the C. sinensis peel by comparison of 3 extraction methods (L 4-6), it is strongly recommended that the introduction of the manuscript consider the different methodologies of extraction of these compounds and not only presents them in the Materials & Methods.

Citations that justify method choices are important. Issues such as: Advantages and disadvantages, possibility of changes in molecules due to the use of solvents, residual solvent, should be considered.

L 67-69: The authors mention "Many in vitro experiments ...", but only present a reference (Rawson, Ho and Li, 2014). Cite more references to substantiate the argument.
Experimental design: There is no bibliographical reference of methodologies for the preparation and extraction of the samples, it is fundamental that they provide them.
Validity of the findings: The practical investigation of the possible industrial applications of these extracted compounds is more innovative and of greater impact than the analysis of the compounds themselves. The latter seems to me very widespread in the literature.
Additional comments: As mentioned earlier, I believe that studies demonstrating the potential of compounds extracted in the industry are more relevant today. However, the investigation in question can be considered relevant for investigating the peel of the fruit and comparing methods of extraction for this industrial waste.


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: PHYTOCHEMICAL COMPOSITION AND IN VITRO ANTIOXIDANT ACTIVITIES OF CITRUS SINENSIS PEEL EXTRACTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors did a great job in this paper.


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

Input:
Title: PHYTOCHEMICAL COMPOSITION AND IN VITRO ANTIOXIDANT ACTIVITIES OF CITRUS SINENSIS PEEL EXTRACTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: All the above considerations were sufficiently answered by the authors.
Experimental design: All the above considerations were sufficiently answered by the authors.
Validity of the findings: All the above considerations were sufficiently answered by the authors.
Additional comments: The authors accepted the suggestions of the review and were enlightening in their amendments. I believe the manuscript is more complete and ready to contribute to the area in which they propose to research.


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: GENETIC DIVERSITY OF MICROSPORIDIA IN THE CIRCULATORY SYSTEM OF ENDEMIC AMPHIPODS FROM DIFFERENT LOCATIONS AND DEPTHS OF ANCIENT LAKE BAIKAL
Review round: 1
Reviewer: 1

Output:
Basic reporting: English – Grammatical errors are present, but should be picked up during editing. I have identified some myself.
References – Some key references are missing, but the style is fine in most cases. The authors sometimes swap between year ascending or year increasing.
Structure – The structure of the manuscript is fine, but sections on statistical analyses are missing, and the phylogenetics needs much more information.
Hypotheses – The hypothesis is interesting, however much work is needed to draw scientific conclusions from the data.
Experimental design: Original – Yes, the work is original and of interest to the scientific community.
Research question – The research question is clear, however it is not fully explored and there is much needed from the authors to make this a publishable manuscript.
Technical and ethical standard – Ethical standard is fine. Technical work seems fine, but more detail is needed in the methods.
Methods – More detail needed. Specifics are listed below in general comments.
Validity of the findings: Impact – Good. Of interest to microsporidian researchers and taxonomists as well as ecologists.
Data – The phylogenetics needs inclusion of taxonomically defined species, such as: Cucumispora dikerogammari; Cucumispora ornata; Cucumispora roeselii; Nosema bombycis; Variamorpha species (several); and members of the Enterocytospora-like clade (clearly displayed in Bojko et al. 2016 and Vavra et al. 2016), including Hepatospora eriocheir and Parahepatospora carcini (if gene sequence data crosses over and is able to align) and members of the Entercoytozoonidae. Please use the Vossbrinck and Debrunner-Vossbrinck 2005 paper on the 5 clades of Microsporidia, defined using molecular phylogeny, where appropriate. The diversity data from your paper needs to be properly analysed. No analysis is present. No significance data is present for DNA similarity: comparison coverage?; e-value?; similarity? All of these are not present and need to be included – All are output from BLAST (NCBI).
Conclusion – Speculative, but the data are not fully analysed and the authors have much to do before this can be properly drawn.
Speculation – Yes. The data are not properly analysed (or at all?). Once this is done I will reassess this when I review it for the second time.
Additional comments: Title: It should be Microsporidia. Capital M.
Line 25: change to ‘microsporidian’
Line 31: When using the phylum name a capital M is needed for Microsporidia. Please change this throughout the manuscript.
Line 32: ‘Microsporidium’ is not a genus within the Microsporidia, it is in fact a holding genus for unassigned genetic data. I suggest rewording this to “ The 20 nucleotide sequences of small subunit ribosomal (SSU) rDNA (681bp) showed similarity to the Cucumispora, the unofficial genus Dictyocoela, and several unassigned microsporidia sequences. These were obtained from…”
Line 34: Alter the text to “Our sequence data show similarity to…”
Line 37: In the haemolymph
Line 36-38: I think you should re-word this to: “The results of our study indicate that microsporidian diversity in the endemic amphipods of Lake Baikal does not corelate with host, geographic location, or depth factors, but remains homogenously diverse throughout.”
Line 41: This initial description of microsporidian taxonomy is misleading. I suggest replacing this first sentence with a more accurate determination of where Microsporidia sit phylogenetically relative to other organisms. I suggest reading the introduction of Bojko et al. 2016, which describes parahepatospora; Stentiford et al. 2015, which describes Paradoxium; and data surrounding the Opisthosporidia, which I believe was published in a 2014 paper by Karpov et al. – Those papers will give you a good foundation for your introductory sentence.
Line 45: The reference is Stentiford et al. 2013.
Line 46: Microsporidian can influence host sex characteristics. Not all do this. The referencing here reverses direction.
Line 47: American English is used? I think the journal requires British English.
Line 51-52: I would just state horizontally or vertically transmitted. Horizontal transmission is not just through food.
Line 52-53: They have been noted to infect…
Line 55: I think you should start your introduction with this line. Then once you get to line 75 add in your paragraph on Microsporidia. This will help your manuscript flow better.
Line 77: microsporidian
Line 83: You should call these ‘gene isolates’ not species. Most sequence data linking to the Microsporidia are yet to have full taxonomic description.
Line 132: This is slightly confusing. Were the haemolymph samples from several amphipods of the same species pooled into a single extraction and PCR? Please be explicit here or refer to where this specific data can be located.
Line 136: DNA extraction, not isolation.
Line 146: This is a lot of dNTP… But if it is correct then I suppose the excess would not have inhibited the reaction in any way. Please check the calculation to be sure.
Line 157: This should be titled “Nucleotide sequence analysis and phylogenetics”. You need to describe your use of BLAST (NCBI), if that is what you used to check similarity to other sequence isolates. Your phylogenetics has a lot that isn’t mentioned. I need to know which algorithm you used to test if your analysis is reasonable… was it Tamura92/Jukes and Cantor/ etc? I need to know if the sequences were trimmed. What the gap costs were. As well as a variety of other information. You can have a look at other studies that display this information to see what is missing. The previously suggested papers will also help with this: Bojko et al. 2016; Stentiford et al. 2015 – Microsporidia descriptions.
Methods: Do you not have any statistical analysis of your data? You should be able to provide a basic analysis of whether there is significant diversity changes between the depths and locations. Perhaps use Simpsons Diversity Index and then compare using an ANOVA, if the data are normal.
 Line 165: remove the “have”.
Line 168-169: Refer back to my comment above about these “genera” and adjust your statement accordingly. Microsporidium = holding genus. Dictyocoela = unofficial genus. Cucumispora = fully characterised genus.
Line 171-174: This is unclear. Do the authors mean that only one genetic isolate was detected from each positive sample? If so, this should be stated clearly.
Figure 2: The description of this figure needs altering. Cucumispora was described by Ovcharenko et al. 2010, followed by the second description of a species in this genus by Bojko et al. 2015, followed by a third description in Bojko et al. 2017, who also developed a phylogeny exploring the additional sequence isolates that likely belong to the Cucumispora. You should utilise these three references in combination when explaining your phylogeny, because the background data will help you describe the position of your new isolates.
Figure 1: You need to list the tool you used to make your map. You should also show all the places you collected and tested amphipods for Microsporidia. This negative data is also useful. Perhaps list the sites with Microsporidia in red or with a red dot.
Figure 2: This figure is missing almost all of the taxonomically identified species sequence isolates. For example, you have not included Cucumispora dikerogammari (see Ovcharenko et al. 2010), Cucumispora ornata (see Bojko et al. 2015) or the most recent Cucumispora roeselii (see Bojko et al. 2017). For the Dictyocoela, you have not provided the sequence of D. berillonum or many others. Your section ‘M’ should not be called Microsporidium. This group is explored in Bojko et al. 2016 and you should include the same isolates, such as Globulispora mitoportens, Parahepatospora carcini, Hepatospora eriocheir, and many many other fully described species. You cannot provide a readable tree unless you are using these known species as anchors to view your phylogeny. In essence, your phylogenetic tree needs completely re-doing with the inclusion of many known Microsporidia for which sequence data is available. I also suggest using a combination of Maximum Likelihood and Bayesian methods, or Neighbour Joining to give two perspectives on the data. You can also use Bojko et al. 2016 to help you to see how this should be displayed.
Line 172: This is a phylogenetic tree. Dendrogram, cladogram etc are confusing and I would stick to this terminology throughout.
Line 182: You should include these sequences. It will make your phylogenetic tree much better and informative.
Line 188: From the unofficial genus, Dictyocoela. This genus is awaiting full taxonomic confirmation. Also, “found earlier”.
Line 192: remove the macronuclear
Line 194: This is not a cluster of Microsporidium, essentially here you are detecting isolates that clade with the Enterocytospora-like clade, the Enterocytozoon genus and the Enterocytozoonidae. When you include many more of the described Microsporidia in your tree you will be able to compare your tree to that of other studies.
Line 195: species should not be in italics.
Line 203-206: You will need to alter all this information based on the outcome of your phylogenetics when you include more systematically characterised Microsporidia. The genus Cucumispora was described by Ovcharenko et al. 2010, and further added to by Bojko et al. 2015 and Bojko et al. 2017. Bojko et al. 2017 explored the novel members of this genus using their sequence data as a proxy for taxonomy. In fact, before SSU information was gathered for Cucumispora dikerogammari, the species was named Nosema dikerogammari. Please read Ovcharenko et al. 2010 to see the details and other references.
Line 212: I want to remind you not to use Microsporidium as a group. It is a holding genus for many taxonomically diverse sequence isolates that need full characterisation. This is also mentioned in Bojko et al. 2016 – I strongly recommend that you read the introduction and phylogenetics of this paper.
Line 215: How can an outbreak be accidental? Was it accidentally introduced? Or is it a rare event? If so, how do you know it is rare… there is no continued monitoring of this species and its parasites.
Line 217-219: How can you conclude this is significant if you do not provide any statistical analysis of your data. Also, you pool many of your samples so you cannot give a reasonable estimate of parasite prevalence amongst specific populations, but may be able to provide an indication of species diversity.
Line 220-222: But you state earlier that all the sequences were different? Please be very clear about this.
Line 223: genus Cucumispora. But no, you have found similar sequences – these cannot be added to the genus officially without pathology and lifecycle information at minimum. If they are similar please give the detailed information such as coverage, sequence similarity, e value. This should also be reported in the results for every isolate you find, or at least in a suppl. table.
Line 229: This will be a specific isolate named Microsporidium. Please give the accession number from NCBI and the detailed information such as coverage, sequence similarity, e value.
Line 239-241: This conclusion needs much stronger foundation. Once you address the points I have made above you will be able to draw a relevant and accurate conclusion. Weren’t some hosts the only hosts to have certain Microsporidia? You say this above…
Line 244: The sequence isolates that we have identified during our study…
Suppl. Data: You need to provide data on the number of samples you actually tested. You only give the number of pooled samples. You need to provide similarity data to other Microsporidia gene isolates in the suppl. data or in the text of your report. You also need to provide your accession numbers for your isolates in the suppl. data. The presence of these on your tree is not sufficient as quality can often cause them to be illegible.

My final response:
I would like to review this manuscript again after the above changes have been made and the data analysed. I think this is a very interesting paper with good potential, but it is not valid within the literature in its current state, including: several errors around Microsporidia taxonomy; missing sequence data in the phylogeny; and no visible statistical analysis of the diversity data that you have collected. Much of my own research takes place upon the Microsporidia of amphipods, and much of it is mentioned above – please feel free to use this as a guide to find further literature that will help you to better analyse and discuss your data in this manuscript. Once these edits are completed it will be good to see this manuscript again. I have opted for you to know who I am, so you are welcome to look me up if you have further questions that I can help with.


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

Input:
Title: GENETIC DIVERSITY OF MICROSPORIDIA IN THE CIRCULATORY SYSTEM OF ENDEMIC AMPHIPODS FROM DIFFERENT LOCATIONS AND DEPTHS OF ANCIENT LAKE BAIKAL
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is generally well written. I have some minor issues.

Line 217-219: Generally, by comparing the percentage of infected hemolymph pools of different amphipod species from chosen sampling points (Table S1), we can conclude that the parts of infected individuals can vary significantly.

I don't think I understand what the authors are saying here. What do they mean by 'parts of infected individuals'? It sounds like they mean different tissues. If so, how does the percentage of infected hemolymph pools from different amphipod species show this?

I think this section needs rewording to make sure the point is clear.

Line 249-251: However, search for microsporidia in amphipods from higher depths (200-1600 m) is still necessary to confirm the observed homogeneity in distribution of these parasites.

I think ‘search for microsporidia in amphipods at greater depths’ or ‘search for microsporidia in amphipods at a greater depth (200-1600 m)’ is probably more suitable.
Experimental design: The authors make considerable play of detecting the presence of microsporidia using the hemolymph

'However, most previous studies utilized the whole individuals or soft amphipod tissues for amplification of microsporidian DNA, which does not rule out the possibility of contamination. To avoid this problem, our group recently conducted a study using molecular genetic techniques (SSU rDNA sequencing) to detect microsporidia in circulatory system of several endemic amphipod species from Lake Baikal (Madyarova et al., 2015). Searching directly in the hemolymph minimizes the possibility of identifying SSU rDNA of microsporidia located on exoskeleton, in gut lumen or inside parasites of the amphipods and can guarantee that the found microsporidia are parasitic directly to the amphipod species studied.'

I have no issue with the authors using the hemolymph but the above statement does raise a question. Is there any evidence that using hemolymph versus soft tissue produces notable differences in infection categorisations? It would be possible to do both types of extraction using the same animals.  Has this been done? I noticed that the recent paper that surveyed infection in Lake Baikal (Ironside and Wilkinson, 2017) removes exoskeleton and gut tissue before using the soft tissue for DNA extraction. So they are also taking steps to try and prevent contributions from the gut and exoskeleton. I tend to agree that taking the hemolymph will reduce the likelihood of contamination. However, is there evidence that it does in practice? Also, are there limitations to using the hemolymph? Different microsporidia vary in their tissue distribution within hosts. Could some microsporidia be found at high levels in the soft tissue but low levels in the hemolymph? Again, a comparison of infections in the hemolymph and soft tissues of the same animals (if this has ever been performed) would be informative.
Validity of the findings: The discussion is relatively brief. The introduction refers to several studies that have looked at microsporidian infections in amphipods from Lake Baikal using molecular methods. (Kuzmenkova et al. 2008, Smith et al., 2008, Madyarova et al., 2015, Ironside and Wilkinson, 2017). However, the findings are only discussed in the context of Madyarova et al (2015). How do the findings change/support the picture provided by these other studies (if they do at all)? The authors describe the recent Ironside and Wilkinson (2017) paper as ‘indicating frequent introductions of the parasites into Lake Baikal ecosystem and high homogeneity of microsporidia between species of endemic hosts in the coastal zone’. Do the findings of infections and various locations and depths fit with this picture? I think a few lines in the discussion might help a general reader understand the relevance of this study within its broader context.
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: GENETIC DIVERSITY OF MICROSPORIDIA IN THE CIRCULATORY SYSTEM OF ENDEMIC AMPHIPODS FROM DIFFERENT LOCATIONS AND DEPTHS OF ANCIENT LAKE BAIKAL
Review round: 2
Reviewer: 1

Output:
Basic reporting: All good.
Experimental design: All good.
Validity of the findings: All good.
Additional comments: Re-review of Dimova et al.
The authors have done a great job of incorporating the new information and I only have a few minor comments to be addressed below.

Minor suggestions:
-	The genus Dictyocoela has now been finally been fully systematically defined. This happened during your revisions and is published under:
Bacela-Spychalska, K., Wróblewski, P., Mamos, T., Grabowski, M., Rigaud, T., Wattier, R., ... & Ovcharenko, M. (2018). Europe-wide reassessment of Dictyocoela (Microsporidia) infecting native and invasive amphipods (Crustacea): molecular versus ultrastructural traits. Scientific Reports, 8(1), 8945.
-	Line 92 and 94: Microsporidia needs a capital M.
-	Line 241-242: This data should be represented in the results first and not just in supplementary information. These are interesting findings and it would be good for you to display them in the results of the main 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: GENETIC DIVERSITY OF MICROSPORIDIA IN THE CIRCULATORY SYSTEM OF ENDEMIC AMPHIPODS FROM DIFFERENT LOCATIONS AND DEPTHS OF ANCIENT LAKE BAIKAL
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript has been improved in accordance with the comments of both reviewers. The authors have made a genuine attempt to answer questions and clarify their writing. They have also altered/added information where asked. The small errors in English and sentence structure have been corrected.
Experimental design: The research question is still well defined. More details on the methodology have been added in response the reviewer’s comments. I believe the description of the methodology sufficient to allow other researchers to interpret the results presented and replicate the work.
Validity of the findings: The conclusions drawn by the authors have now been qualified appropriately and the authors make it clear that more study is required to confirm the lack of correlation. I believe the study adds to the existing literature on microsporidia infection and provides more information about the diversity of microsporidian parasites in Lake Baikal.
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: CORAL RESPONSES TO A REPEAT BLEACHING EVENT IN MAYOTTE IN 2010
Review round: 1
Reviewer: 1

Output:
Basic reporting: Minor editing and modification of figures needed as detailed in annotated pdf of manuscript. Paper largely clear and well-written. Figures are relevant and well designed but in need of a few edits.
Experimental design: The design of the data collection and analysis meet standards of this research community. Analyses and conclusions drawn from them are mostly appropriate, although one analysis (with and without unaffected) should be removed as no justification is given for why unaffected values should ever be excluded from the analyses.
Validity of the findings: Data, analyses, and findings are robust and sound except as mentioned above.
Additional comments: No additional comments


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

Input:
Title: CORAL RESPONSES TO A REPEAT BLEACHING EVENT IN MAYOTTE IN 2010
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a well-written and analyzed assessment of a 2010 bleaching event in Mayotte.  The writing is clear and there is sufficient reference to supporting and relevant literature in the field that places this study in the context of others.  Similarly, the authors have indicated the contribution that their findings making to the gaps in the literature.

The authors report on the statistics of the bleaching event from a wide array of transect and quadrat data and report their findings in terms of both genera and area of the reef.

I think the most significant impact of this study is their use of cluster analysis (fig 7c) to assess the changing outcomes when unaffected colonies are/are not included and when weighted components are included.  This was a really interesting and useful outcome of the data presented, particularly in terms of application to other reef locations affected by bleaching around the world.  I recommend that these findings be incorporated into the abstract in a more definitive way.  This part of the study seems to be "undersold" to me and could be incorported more thoroughly.
Experimental design: The overall design and  explanation of the study is complete and easy to follow and understand.  The statistics used are appropriate.

The study fulfills a gap in knowledge related to reporting and assessment of bleaching events and the susceptibility of genera in the event.  An assessment of a past bleaching event (2010) is especially timely as we (quickly) approach greater frequency of these events.
Validity of the findings: The authors follow the standards of Peer J in terms of a robust data set that has been statistically analyzed and assessed.  The authors do not indicate the impact or novelty of their results, nor do they overly speculate on their findings, however, their conclusions are well stated and associated with their overall research question.

My only suggestions relate to making their figures slightly more clear, as follows:

Fig. 2 - A key is needed for the different reef areas depicted in the map.  What do the "P" on the map refer to? What do the "!" in green on the map refer to?

Fig. 4 - I recommend removing the lines connecting panels a and b.  I do not think they are particularly helpful.

Fig. 5a - Define abbreviation in the legend - perhaps refer to Fig. 3 where complete wording on the legend is provided.

Fig. 5b - Define and/or standardize the abbreviations used on the ternary diagram.  For example what is "fat" - perhaps for simplicity, use first three letters of each genera? I do not believe there would be an duplicates.

Fig. 6a - slightly shift the legend for "numbers" so it does not overlap with the graph

FIg. 6b - Define abbreviation in the legend - perhaps refer to Fig. 3 where complete wording on the legend is provided.

Fig. 7b, d-g - Perhaps show on the same y-axis scale for easier comparison?

Fig. 7c - Can the authors make this panel larger? It is difficult to read and is a bit blurry.
Additional comments: I have the following suggested edits to the overall text:

Line 67: change "through have a" to "because of its"

Line 80: change "followed" to "following"

Line 97: change "from" to "on"

Lines 112-113: change to read - "...with 25-m transects (Table 1).  The smallest sampling was a 7-m belt transect and 2 m2 quadrats..."

Line 114: change to read - "... samples of 11 small and 86 large corals were recorded within a 25-m..."

Lines 119 and 121: delete open and close parentheses "()"

Line 137: correct type to read "monitoring"

Line 140: Change to read "...and second, the effect..."

Line 143: I'm not sure what was meant by "analyses were trialled"?

Line 156: Add hypen to "Thirty-four"

Line 182: Delete typo after "following"

Line 197: Delete "to"


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: CORAL RESPONSES TO A REPEAT BLEACHING EVENT IN MAYOTTE IN 2010
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall the authors did an excellent job of writing clearly and reporting the work that they conducted. I thought the figures were very clear and easy to interpret.
Experimental design: The design of these experiments are good. The authors fully explained their design and the context of their results.
Validity of the findings: These results are interesting. While bleaching at Mayotte in 2010 has already been documented, I think that the addition of the size class data is novel and an important aspect of bleaching that is under reported. I also hesitate to predict mortality, however the authors have done a good job of putting that analysis into context and provided adequate explanation of the methods of their estimation.
Additional comments: Overall I found this to be an interesting paper. The surveys were conducted well and were done extensively for this island. The bleaching event was put into appropriate context both across time at Moyotte, and in the context of the recent global bleaching events.

Here are a few specific comments of typos or unclear writing for the authors:
Abstract
Line 35-37. This sentence is unclear. Rewrite for clarity.
Introduction
Line 43. No need for a comma here
Line 55. Insert “of the” into this sentence. It should read “…, with most of the world regions predicted..”
Line 67. Replace “through having” with “since it has”
Results
Line 182. There is an extra f at the end of following
Discussion
Line 241. When you say “This paper”, it is not clear if you mean your manuscript or the paper that you describe just before this sentence. Edit for clarity.
Line 350. Delete “the”, you have two of them in this sentence
Conclusions
Line 373. Remove “and” from this sentence.


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: HPO2GO: PREDICTION OF HUMAN PHENOTYPE ONTOLOGY TERM ASSOCIATIONS FOR PROTEINS USING CROSS ONTOLOGY ANNOTATION CO-OCCURRENCES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well structured. Has a good introduction and a background. References are adequate for the most part. But the writing is not clear at times (some sentences are too long etc.). It is suggested that the writing be reviewed by a native English speaker for improving the readability. Figures are relevant, high quality, well labelled & described (except for Fig 5, which is of poor quality). Raw data are accessible and reasonably well documented. Following is the list of all issues (starting with their line numbers).

Major comments:
Introduction: missing description about sub-ontologies of HPO. Mention the DAG structure of HPO. Are there evidence codes in HPO?
Method, Dataset construction: Which sub-ontologies of HPO are used for your work?

Minor comments:

18: change “provided” to provides
35: change “beat” to beats
46: change “and etc.” to etc.
50: change “source of” to sources of
81: change “basic” to a better word
96: change “with annotation” to with the annotation
103: change “CAFA organization have” to has
121-124: Sentence is too long and does not make sense. Please reword.
133: change “approach” to approaches
134: change “coverage of especially” to coverage, especially
143: change “consist: to consisting
143: define PPIs
155-156: this sentence is not true. RANKS, PHENOStrcut, dcGO are not among the top performers of CAFA2. In fact, RANKS and PHENOstrct did not participate in CAFA2 (Jiang et al., 2016).
164: citation is required to a study showing this bias
165: “concept” may need a better word for this as the meaning of the sentence is not clear
187: change “as for example” to for example
188: “problematic version” requires a different phrase to improve meaning
193-194:  “The function usually..” -  how do you know for sure?
201:  “time-held” may need a different word since this word is not used often
220-221: this sentence suggests that ancestor terms are not reliable – which is not true. May need to reword.
237: change “whole” to complete
243: change “probable to for” to “probable for”
244: “randomly occurred mapping” may need to be replaced by better wording
245-247: need a citation for the sentence starting with “For each ..”. It looks like your equation (1) is based on information gain.
300: change “participate to” to “participate in”
320-324: Define Tau in equations 2, 3 and 4
335: change “obtains” to obtain
365: change “displays” to display
368: change “leaves” to leave
370: change “shows” to show
374: period instead of comma at the end of sentence
431: Wrong name of GO term used for GO:0045728
432: “GO:0045728 which is related to the mapped term GO:0045730 on the GO DAG:. Explain how these two terms are related and specify the relation type.
503-507: “prediction results are available” on 503 and “results not been announced “ on 506 conflicts with each other. Also, “small difference” does not make sense. Elaborate more.
513: “quite limited”: provide evidence
Fig 5 is of low quality – reproduce.
Experimental design: Clearly specify how “genes_to_phenotypes” were created by the HPO curators. Isn’t it possible that some of the same resources/information used for adding GO annotations is used for this (by HPO curators)? If so, your experiments are biased. If not, clarify.

312: It is stated that for the CAFA2 comparison, HPO2GO mappings were re-generated with training data. Does that mean you used both GO and HPO from 2014 Jan?

Following three reasons invalidate the CAFA2 comparison results (Figures 5 and 6). This reviewer feels very strongly about correcting these issues before accepting the paper (because Figs 5 and 6 provide the primary evidence that HPO2GO is effective).

1.	464: Do you use GO annotations from the same period? If not, the results are invalid because you are using 3 years’ worth of GO annotations that were inserted to GO database after the submission deadline (for which the other teams did not have access, regardless of whether they used GO as input or not)

2.	Also, it says the CAFA2 training data is from Oct 2015. According to CAFA2 paper (Jiang et al., 2016), they are from Sep 2013. If this is the case, this is another reason that invalidates results.

3.	476: Clearly mention that you are using “No knowledge” mode. Are you using the exact same evaluation method used in CAFA2 that uses bootstrapping (Jiang et al., 2016). If not, results are invalid. If you did use the same method, clarify.

365: states that you used different n values in Figure 3. Explain why you chose n=1, 5, 25, and 75 in Figure 3. Also, there is another explanation in line 398 that these values “indicate the distribution differences at extreme cases”. Explain how these cases are extreme.

416: in section “The biological relevance of the selected HPO2GO mappings - A case study”, you have chosen only two different examples. Explain why you chose these two examples. E.g. was it because of the high S value?

Explain why you did not use TAS and IC codes for GO annotations (they are used in CAFA2 evaluation)

You should use other measures in addition to Fmax too (Smin and term-centric measures). According to CAFA2 paper (Jiang et al., 2016), there is large variance in ranking of methods when using different measure (for HPO).
Validity of the findings: 35, 482: Due to the issues in experimental design mentioned above, your claim that HPO2GO “beats all other top performers” cannot be considered valid.

573-575: “This approach can easily be translated into novel HPO term predictions for genes/proteins, as well as into new HPO-disease or gene-disease associations.”: Not enough evidence provided in the paper to make the second part of the claim.

582-583: “The methodology proposed here was only meant to support the already established approaches (e.g., text mining), since different techniques with different data sources and perspectives produce results that complement distinct missing pieces of the knowledge space.”: not enough evidence provided in the paper to make this claim (no comprehensive experiment /study for making this claim).
Additional comments: It would be nice to see an analysis of which proteins were missing predictions from your method (evidenced by C = 0.97) and provide insights/ reasoning on why.

It would be interesting to mention how many methods (you compare to) use GO as input.

It would be Interesting to see a comparison of performance between raw mappings vs finalized. This should highlight the importance/ impact of your sampling method.

489: “however, these mappings produced performances slightly inferior to the one generated using the optimal thresholds”. It would be helpful to have a discussion on this observation and why this happened.


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: HPO2GO: PREDICTION OF HUMAN PHENOTYPE ONTOLOGY TERM ASSOCIATIONS FOR PROTEINS USING CROSS ONTOLOGY ANNOTATION CO-OCCURRENCES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript describes an approach to generate cross-ontology
mappings from HPO to GO in order to propagate GO annotations to HPO
annotations, increasing coverage of HPO annotations. The mappings are
created by first using a Jaccard-like measure based on shared genes
between GO and HPO gene sets. Threshold filters are determined using
randomized data.

The approach shows better performance on CAFA2 HPO prediction tests
measures than all other methods. However, as to be expected with any
guilt-by-association method the overall accuracy is low, which limits
the applicability of the approach in real-world applications.

The approach is clearly explained, the author does a good job of
presenting background material. The fact the approach outperformed
existing CAFA2 methods is commendable. However, there needs to be
better biological evaluation of the mappings. Additionally, further
experiments with different scoring measures and annotatuon propagation
would benefit the work greatly, but are not strictly required so long
as the limitations are clearly explained.
Experimental design: My comments are ordered from most important to least important

1. The evaluation of biological relevance is incomplete.

The author performs two evaluations, one using CAFA2 and the other by
examining selected mappings and comparing against the literature. The
The first evaluation is objective and clear, the second evaluation is
problematic.

First, only two mappings are selected and it's not clear if these were
cherry picked. Given there are ~46k mappings it's relatively easy to
pick a handful that have a good story.

The first example has a mistake that should be fixed. The match for
"absence of bactericidal oxidative respiratory burst in phagocytes" is
actually to the less precise "respiratory burst" than "respiratory
burst after phagocytosis" as the authors claim.

But the real problem is that if a set of mappings were selected at
random and then evaluated it would reveal that many of the mappings
are for pairs terms that don't appear to be related in any way, and
genes are shared by chance.

For example, the following two mappings have relatively high scores,
in the top 3% of the complete set of mappings:

HP:0000006-Autosomal dominant inheritance       GO:0005515-protein binding      0.5850
HP:0000007-Autosomal recessive inheritance      GO:0005515-protein binding      0.5734

It's hard to see any biological justification here, and both HPO
inheritance terms and protein binding appear multiple times. If these
were to be used as a basis for suggesting new annotations the false
positive rate would be too high for this to be useful.

To rectify this: minimally, an ubiased sample of mappings should be
randomly selected and evaluated. This could be done from different
score bins.

Additional experiments would be to see how well HPO2GO augmented
annotations would perform on tasks the HPO is designed for such as
disease diagnosis.

2. The decision to use only asserted annotations is not well justified

The manuscript states:

220 as well. In this study, the asserted annotations are used in the analysis (in terms of both GO and
221 HPO), in order to make sure the training set includes only the most reliable annotations.

It is not true that logically propagating annotations up to the root
would have produced less reliable annotations. In fact these are
logically guaranteed to be correct. Eliminating this would reduce
recall with no gain in precision.

I recommend that the experiment is redone using propagated
annotations.

Failing this, the manuscript should explicitly state the lack of
propagation as a limitation, or provide a valid reason for excluding
them.

3. The decision only to use experimental GO evidence is not well
justified

This is related to the previous point. The previous point concerned
logical propagation up the hierarchy which is always guaranteed to be
valid, for HPO or GO. This point pertains to the propagation of GO
annotations from other species. In this case, propagation is not
guaranteed to be valid (due to species difference, natural evolution,
etc). However, the complete set of GO annotations are generally
regarded to be a good default choice, evidence codes such as ISS and
IBA are high quality, and methods such as propagating based on
interpro2go are reliable.

I think the results would potentially have been better had these been
included. Ideally there would be an experiment comparing the two.

I recommend including these, or alternatively more clearly stating
that this is a limitation of the approach, or providing clearer
justification for the current choice.

4. Comparison with logical definitions

The HPO includes manually curated OWL definitions in which HPO classes
are connected to GO, Anatomy ontologies, etc. An obvious test is to
validate the predicted HPO2GO against this manual one.

The manuscript states:

516 community. It would also be interesting to compare the HPO2GO mappings with the
517 abovementioned manually curated associations; however, it is not possible to access this data in
518 the HPO repository anymore.

In fact these are now part of the official OWL version of HPO.

5. Choice of scoring

The scoring method (Eq1) is similar to Jaccard, but also uses a
statistical procedure to see thresholds of number of genes and
scores.

It's not clear why a straightforward fisher exact test is not used or
compared against. This has the advantage of providing a p-value for
each mapping indicating the probability that such a mapping would be
observed given the null hypothesis. Standard multiple hypothesis
corrections methods can be used.

It may be the case that Eq1 has some advantages but additional scoring
methods should have been explored.
Validity of the findings: See section 2
Additional comments: The discussion section is a good overview of some of the challenges,
and demonstrates the author has understood some of the nuances of
predicting HPO annotations, and why simple approaches like BLAST would
have low precision.

e.g.

557 Due to this reason, transferring
558 a HPO annotation from one protein to another based on sequence similarity does not have a
559 biological relevance, which explains the poor performance of the BLAST classifier.

This is a great suggestion:

589 As for the future work, it is first planned to map the HPO terms to GO term trios (i.e., MF, BP and
590 CC terms at the same time) using enriched annotation datasets, as explained at the Discussion
591 section


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: HPO2GO: PREDICTION OF HUMAN PHENOTYPE ONTOLOGY TERM ASSOCIATIONS FOR PROTEINS USING CROSS ONTOLOGY ANNOTATION CO-OCCURRENCES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Thank you for carefully addressing all my comments.


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

Input:
Title: DETECTION AND BENCHMARKING OF SOMATIC MUTATIONS IN CANCER GENOMES USING RNA-SEQ DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Clear and professional English language used throughout the article. Literature references are not sufficient in the paper. For example, line 44: you referred to several studies without references. On line 53 provide the reference for MuTect2 (Cibulskis
et al., Nature Biotechnology, 2013) although you provided it on line 116.Please add references when needed.
Figure 3 (A and B) is really small and it is difficult to see the different variant features. Please improve it.
Experimental design: Primary research is within scope of PeerJ as it is a research article. The paper presents a pipeline for processing RNA-seq data from glioblastoma multiforme tumors in order to identify somatic mutations and entails the use of the STAR aligner 2-pass procedure jointly with MuTect2 from GATK to detect somatic variants.They compared the performance of their pipeline to whole-exome sequencing.
Validity of the findings: RNA seq can give similar results than WES under certain conditions and this article provides another example for it.
In the results section, read counts and variant features highlight differences between RNA-seq and WES variants in TCGA samples, the author wrote line 218: “The RNA-seq/WES intersection was enriched in variants from coding regions (89.7% of coding variants), which was probably induced by a higher coverage overlap”. As RNA seq captures RNA, introns, exons, the RNA-seq/WES intersection is located in the CDS.

In the paragraph called “allele fraction and coverage are useful features to further classify variants” (line 225-239), did the authors checked whether reads supporting some of the high coverage low AF variants found with RNA-seq / not with WES could be found in the alignment files and did the authors try alternative variant callers that are highly sensitive at low AF frequencies, e.g LoFreq?

Wilm et al. LoFreq. (2012). A sequence-quality aware, ultra-sensitive variant caller for uncovering cell-population heterogeneity from high-throughput sequencing datasets. Nucleic Acids Res.; 40(22):11189-201.
Additional comments: The paper entitled “detection and benchmarking of somatic mutations in cancer genomes using RNA-seq data” develops and evaluates a pipeline for processing RNA-seq data from glioblastoma multiforme tumors in order to identify somatic mutations compared to whole-exome sequencing. The pipeline entails the use of the STAR aligner 2-pass procedure jointly with MuTect2 from GATK to detect somatic variants. The overall level of the manuscript is good: even if it is quite simple, it is well written and some important considerations are highlighted. In the following, there is a list of points that the authors should answer:
 (1) did the authors checked whether reads supporting some of the high coverage low AF variants found with RNA-seq / not with WES could be found in the alignment files and did the authors try alternative variant callers that are highly sensitive at low AF frequencies, e.g LoFreq?
(2) add references in the paper
(3) do the figure 3 to improve its size and readability