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Dear Jane and colleagues, Congratulations on this outstanding research work. Your research results will serve as a great information for peers and Forest Pathology community. Job very well done.
Best regards
Simon
Simon Francis Shamoun
Academic Editor, PeerJ
[# PeerJ Staff Note - this decision was reviewed and approved by Konstantinos Kormas, a PeerJ Section Editor covering this Section #]
Dear Dr. Stewart,
Based on the reviews of three external reviewers and my own assessment, your manuscript still need a "Major Revision" before accepting it for publication in PeerJ. Please, address all the comments and suggestions that were raised by the reviewers and submit a "Revised Version" to PeerJ for further action.
Thank you for submitting your research results to PeerJ.
Best regards,
Dr. Simon Francis Shamoun
Academic Editor, PeerJ
[# PeerJ Staff Note: It is PeerJ policy that additional references suggested during the peer-review process should only be included if the authors are in agreement that they are relevant and useful #]
Overall, the ms is clear. I noticed few parts that need to be clarified.
Table 3 should be rededisgned and improved with more information.
Major point is about the working hypothesis. They need to be restated in something more clear and precise. Please, see all the details about that in my general comments below
No major problems with that. I added few suggestion to explore further the data and help presenting the results
All required data have been provided. No issue with this point
Review of PeerJ manuscript 57289v1 by Ata et al.
So glad to see this manuscript on this pine-needle disease that is becoming every year more noticeable and problematic. The authors provided a first molecular assessment of the Lophodermella genus (five species out of the nine described), addressing questions about the relationships between the different Lophodermella species and other Rhytismaceae species, and the relevance of morphological characters, to delineate this genus. Another important aspect of this work is the release of the first Lophodermella DNA sequences (3 loci) into public sequence databases, making a reference set for future taxonomical and eDNA studies. One next step will probably be to enrich this first set with DNA sequences from type or voucher specimen from herbaria – but this is not the point here.
Although the manuscript is overall well written and organized, I still have some major points and few questions/suggestions that hopefully will help improving the clarity of the work.
1 - The authors examined relationships between Lophodermella spp. and other Rhytismaceae species. Unfortunately, the loci sequenced are not resolutive enough, and the concatenated tree has a large polytony on its basis. This is recurrent problem with fungal phylogenies (see my comment about the LOD group and L. conjuncta in the next paragraph below) and there is different reasons for that, such as a lack of informative characters, homoplasy… I don’t disagree with the way the authors tackle it on L266 by saying that more sequencing should help, but I think they should explore the problem a bit further by looking at the level of homoplasy in their sequence alignements. One way to reduce homoplasy is to analyse different partitions in protein-coding genes (in this case the EF1 locus). Analyzing only the first and second nucleotides (i.e. discarding the third nucleotide) at each codon in EF1 could result in a tree with higher resolution as these two nucleotides are less prone to multiple and reverse mutations than the third one (because of codon degeneracy).
2 - The rationale for elucidating the phylogenetic relationships between the Lophodermella genus and other Rhytismaceae is not clearly introduced. The authors states in the introduction that they aim “resolve the classification of species closely related to Lophodermella (and the case with Lophophacidium dooksii is well presented) and to “elucidate” the phylogenetic relationships of Lophodermella spp. with other rhytismataceaous species (L92-93). This is OK, but these are very general statements. I think adding a clear hypothesis (or aim) at the end of the introduction would help here. As the genus Lophodermella was defined on the basis of shared morphological characters between species (see L68-70), we would expect that this genus is monophyletic. Then, a second objective should be added i.e. examining the relationship and diversification withing the Lophodermella genus and if the species delineation following some morphological criteria (which is not discussed) and host specificities (which is discussed in the Discussion section L352). Also, I found it very surprising that the relevance of the morphological criteria that distinguish between Lophodermella species (presented in Table 2) is not discussed in the Discussion section.
3 – Table 3 contains the non-Lophodermella sequences downloaded from NCBI-nr used in this study. On which basis were these species/isolated selected? Are they the only Rhytismaceae sequences available on NCBI-nr? are they all pine infecting pathogens and/or endophyte. More info about that would be helpful for the understanding of the aims of the authors in using these sequences. In addition, the information about host, disease, lifestyle (if available) should be added in Table 3.
4 - Data obtained by the authors suggest that the Lophodermella genus is polyphyletic. I wasn’t completely buying it (thinking it could just be caused by homoplasy) till I looked in details into the sequences provided in the Supplementary material. At the three loci, L. conjuncta sequences are quite different of other Lophodermella species and share a lot of synapomorphies with other Rhysticimaceae species. I guess, nothing new here: it is not the first time that a fungal genus defined with morphological criteria is broken into different pieces with molecular data. However, I still have few questions/suggestions about that: first, all the phylogenetic trees presented in this manuscript are majority rule consensus trees (generated from the bootstrap analysis). The ML analysis usually results in a “best” tree. What were the “best” tree looking like for each locus? what about the concatenated dataset? was the LOD group and L. conjuncta resolved on a same node? This information can be useful as the “best tree” represents the most likely tree (of all the tested trees) given the data. The best tree should be presented in Figure 2 (instead of a majority rule consensus tree from the Bayesian analysis) and the BS obtained after the bootstrap analysis in ML and the PP from the Bayesian analysis should be reported at each node of the tree. Same thing for Fig. S1 to S3.
In addition, I think that making a new figure or supp. figure showing a matrix of distances (or nucleotide identity) between pairs of species within the Lophodermella genus (for the concatenation of the ITS, LSU and EF1 loci) would be very helpful to convince the reader of this strong “divergence” between species of the LOD group and L. conjuncta; then, the reader wouldn’t had to dig into the sequences as I did. For example, the nucleotide identity in the EF1 loci between species of the LOD group is in the >90% while the identity with L. conjuncta is around 70-80% - this is quite a difference. I’d also suggest to add into the matrix one or two Lophodermium or Elytroderma species as a “control”; I suspect the distance between species of the LOD group and Lophodermium sp. should be in the same range than the distance between species of the LOD group and L. conjuncta. If that can help, I have one of these distance matrix in one of my old paper: https://www.sciencedirect.com/science/article/abs/pii/S0953756209000495?via%3Dihub - Fig.3).
5 - I really liked the approach (and I think the authors did a great job here) of reconciliating molecular characters with morphological characters by mapping them back to the phylogeny. However, what I do not clearly understand is why it was only done for the whole Rhystimaceae dataset? There are some characters for each Lophordermella species in Table 2. Why not reconstructing a Lophodermella phylogeny rooted with Lophodermium and/or Elytroderma only, and map these morphological characters and host specificities on this new phylogeny (and discuss if they make sense)? In this way, we could see if a dichotomous key based on these morphological characters can be used in practice to ID these different species. As stated above (at the end of point #2) the relevance of the morphological characteristics of each Lophodermella species (Table 2) should be discussed in the light of the phylogenetic results obtained in this study. The authors did a great job in gathering this information in Table 2 and should use it.
Other comments :
L54. P. contorta => Pinus contorta
L56. Pinus contorta => P. contorta
L70. change « a closely » for “the closely”
L91-93. Weird sentence with two ideas in it. “are important in identification”, of what? Please, rewrite.
L91. Which db do you mean by “fungal genetic databases”? Is it NCBI-nr.
L97. What about the four other species. Is it because their distribution doesn’t fit NA and EU (e.g. L orientalis in Asia) and/or they are very uncommon (and you were unable to obtain samples)? A better idea about the host range/distribution of some of these species should be provided in the previous paragraph when mentioning the nine different known species (L66). Host specificity provides (in some case) one more traits that allow to distinguish between these species; e.g. P. mordida and P. cerina on P. ponderosa; L. maureri on P. ayacahuite in Mexico
L99. If I clearly understdand, the aim here is to use molecular phylogenies to guide the identification of shared “morphological” traits between these different species. If so, I should be probably stated in a clearer way.
L.188. “for most”. What do you mean by most; how many sample corresponded to mix of different individuals; were they discarded?
L190. was it systematically the same amplicon size for the five different Lophodermella species. Based on the sequences fiund in the supp. mat., I guess no.
L200. Doesn’t really make sense to talk about the tree built from the concatenated dataset before having presented the result of the partition homogeny test (L208).
L208. The ILD test informs about character congruence between the different partitions, which is accurate, but this is not a topology test. See https://www.sciencedirect.com/science/article/pii/S153204640500081X.Topological congruence between the three dataset should also evaluated. There is some tests for that or there is the “good old way” of just checking if the three tree have some nodes differences (after boostraping).
L220. “clustered at ITS… » I see what you mean, but actually that means nothing. Something like that would be better: RMNP_01 and L. dooksii were found into a cluster supported with xx BS and xx PP in the ITS tree and ….
L241-244. It would be nice to explain (for the non-specialist) what these RI and CI indexes exactly are – or what do they mean.
L278-283. long sentence with several ideas in it. + I’m not sure I understand what you mean here: “since Lophodermella is an understudied genus where molecular studies are rare”. Please, rewrite –with few shorter sentences
L283. “Lophodermella species with no molecular information”. You mean: by including Lophodormella species for which (so afr) there’s no sequence data available? Please, clarify
L289. “Though morphological distinctions between the two species are poorly defined”. Actually, Table 2 suggests that there’s some difference for several morphological criteria. E.g. range in ascomata size. To me that looks quite well defined, the issue being the overlap in size observed for most of them.
The article is well written and I have no major criticisms on the structure of the text, figures and tables. I think Fig. 3 would be improved by the inclusion of scale bars to provide a size reference.
L61-62: There is a published report of a prior outbreak of L. cerina in the southern U.S.
(Czabator, F.J., Staley, J.M., and Snow, G.A. 1971. Extensive southern pine needle blight during 1970-1971, and associated fungi. Pl. Dis. Reporter 55: 764-766.)
The experimental design appears sound and the authors were very thorough in analyzing the data.
L163-167: It’s been noted for many years now that model selection for phylogenetic reconstruction may not be necessary and that the most parameter-rich model (GTR+I+G) can be utilized to provide the best results. A recent publication discusses the issue more carefully (https://www.nature.com/articles/s41467-019-08822-w)
L168: why only 200 BS replicates for ML when 1,000 replicates is the standard?
This study is laying the foundation for future work that can delve more deeply into possible cryptic species and host distribution with a larger dataset. It's a bit surprising how poorly studied this fungus is and the authors really had no access to additional data from the various databases. The authors did a great job of interpreting their findings while avoiding speculation not supported by the data.
L174-175: Personally, I think too many outgroup/related sequences have been included, which I see is largely based on Laflamme et al. (2015). I can understand the use of closely-related needle blight pathogens of conifers (e.g. Lophodermium, Lirula and Elytroderma) but many of the >50 sequences may not provide any additional resolution, especially in the consensus tree format. Specifically, the “fungal endophytes” should be removed and species of Hypoderma could be reduced. Also, correct spelling on L. piceae.
L218-219: The isolate code (RMNP_01) is not included in Fig. 2.
L278-280: You elude to it here, but I think you should state it more clearly: based on the data presented here, it’s possible that L. conjuncta is not a true Lophodermella and may need to be reclassified. It’s possible that these isolates represent a segregate genus that shares a close morphological and phylogenetic relationship to Lophodermella.
Overall, I enjoyed reading this manuscript and I commend the authors on their fine work. I have only minor suggested edits.
The manuscript is mostly clearly written. There are some sections that need clarity and some where the grammar can be improved upon. These sections have been highlighted on the attached document.
The introduction provides a solid background for the study. The distinct lack of molecular data available for pine needle pathogens in the Rhytismataceae is highlighted and forms the basis of the study.
Tables are sufficiently detailed and contain all the necessary information needed for the study including data summaries. Some, such as Table 1, are quite long and can be re-arranged (without losing content) to reduce the length for more efficient reading. Table 3 could possibly be moved to supplementary data.
In Table 2 – I would suggest the authors include the descriptions and measurements for the undescribed Lophodermella sp. This would be useful for future studies. Ideally this table should contain this information for all 9 described Lophodermella species.
Figure 1 could do with some re-sizing and re-formatting to produce a proper photo-plate.
The main focus of the paper is to characterize the Lophodermella species causing disease in the USA and Europe, mainly using molecular methods. In this regard, this paper goes a long way in trying to reduce the void of sequence data available for some of the species in Lophodermella and this is commendable.
However, my biggest concern with the paper is the lack of completeness of the phylogenies in terms of species of Lophodermella being represented. The authors say there are 9 species (lines 66) and but only 5 of the species are sequenced. Is there no chance to get the other species in Lophodermella to complete the phylogeny for all the known and described species in the genus? My concern is that, for example, the potentially new Lophodermium sp. identified in this study could actually be one of the other species (e.g. L. cerina, L. maureri, L. morbida or L. orientalis). If not to be included then the authors should try and motivate why these species should be ruled out as a possible id.
The lack of sporulation of spores on media is interesting to report and is probably the reason why so little molecular work has been done on this genus.
Line 146: Does this reference include the protocol i.e. reagent mixes and pcr cycling conditions which are missing for the PCR amplification steps.
Line 153 samples: what is considered a sample here from the 32 collections across 12 sites?
For the ITS region – the authors need to stipulate if both the internal transcribed spacer regions (1 and 2) were used or just one of them?
There is a section on sampling missing in the results. If these are emerging diseases, a description/incidence/severity report etc of the disease would be good.
There is a mixture of the use of term haplotype and genotype in the text.
Table S1 – This table is not very clear in its headings (see comments on file). Is it not clear to me how many isolates of each species were sequenced and then which were used for blast searchers - OR were all the sequences for a particular species identical?
All data has been provided and is sound. The discussion is comprehensive and informative and relates back to the results. Clear reasonings are given as to why the authors have not gone ahead and described the new species. Clarity is still needed regarding officially transferring Lophophacidium dooksii to Lophodermium dooksii.
Additional comments for review can be found directly on the PDF.
The paper will make a great contribution towards furthering our knowledge on pine needle diseases and the pathogens that cause them.
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