Draft genomes, phylogenomic reconstruction and comparative genome analysis of three Xenorhabdus strains isolated from soil-dwelling nematodes in Kenya

  1. Ryan Musumba Awori
  2. Charles N. Waturu
  3. Sacha J. Pidot
  4. Nelson O. Amugune
  5. Helge B. Bode

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Abstract

As a proven source of potent and selective antimicrobials, Xenorhabdus bacteria are important to an age plagued with difficult-to-treat microbial infections. Yet, only 27 species have been described to date. In this study, a novel Xenorhabdus species was discovered through genomic studies on three isolates from Kenyan soils. Soils in Western Kenya were surveyed for steinernematids and Steinernema isolates VH1 and BG5 were recovered from red volcanic loam soils from cultivated land in Vihiga and clay soils from riverine land in Bungoma respectively. From the two nematode isolates, Xenorhabdus sp. BG5 and Xenorhabdus sp. VH1 were isolated. The genomes of these two, plus that of X. griffiniae XN45 – this was previously isolated from Steinernema sp. scarpo that also originated from Kenyan soils – were sequenced and assembled. Nascent genome assemblies of the three isolates were of good quality with over 70 % of their proteome having known functions. These three isolates formed the X. griffiniae clade in a phylogenomic reconstruction of the genus. Their species were delineated using three overall genome relatedness indices: an unnamed species of the genus, Xenorhabdus sp. BG5, X. griffiniae VH1 and X. griffiniae XN45. A pangenome analysis of this clade revealed that over 70 % of species-specific genes encoded unknown functions. Transposases were linked to genomic islands in Xenorhabdus sp. BG5. Thus, overall genome-related indices sufficiently delineated species of two new Xenorhabdus isolates from Kenya, both of which were closely related to X. griffiniae . The functions encoded by most species-specific genes in the X. griffiniae clade remain unknown.

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  1. Version published to 10.1099/acmi.0.000531.v4 on Access Microbiology
  2. Access Microbiology

    In this manuscript version, Awori et al. have applied the minor changes suggested for acceptance. I would like to thank the authors for minding he comments of the reviewers and myself. Congratulations!

  3. Version published to 10.1099/acmi.0.000531.v3 on Access Microbiology
  4. Access Microbiology

    In this revised manuscript, Awori et al. present the analysis of various Xenorhabdus genomes introducing the modifications suggested by the reviewers. After these changes, the manuscript has improved its quality and is now in the position to be accepted for publication. Congratulations to the authors for this piece of work. Nevertheless, there are two minor aspects that the authors might have overlooked during the corrections: • After comment 4 of Reviewer 2, the authors corrected the terminology from Xenorhabdus sp. nov. BG5 to Xenorhabdus sp. BG5. However, there is still one reference to Xenorhabdus sp. nov. BG5 in the Figure 4 legend (L 459-464) that the authors might have missed. Please consider a correction. • In the text modification introduced after comment 19 of Reviewer 2, the authors mention that this phenomenon of inflated counts due to enrichment in secondary metabolite related genes at the boundaries of contigs is frequent. It would be ideal if you could support this statement with at least one reference. Please consider these minor issues in a second revised version before progressing the manuscript to accepted for publication. Again, I would like to congratulate the authors for this final piece of work.

  5. Version published to 10.1099/acmi.0.000531.v2 on Access Microbiology
  6. Access Microbiology

    In this manuscript, Awori et al. present the analysis of various Xenorhabdus genomes. As this bacterial genus can be the source of potential antimicrobial compounds, the description of new species does have an urgent interest for the scientific community. The topic is introduced well and the overall methodological approach and result interpretation seems fairly well performed. The manuscript has been reviewed by two experts in the field and their reviews are enclosed. However, as spotted by the reviewers, several nuances must be introduced. Moreover, various points for the methodology and the results would need further clarification, and a number of statements need to be softened to properly reflect the results. Please consider the reviewers’ comments thoroughly and address their concerns point by point in a separate document. A revised manuscript should include appropriate revisions.

  7. Access Microbiology

    Comments to Author

    In this manuscript, Awori et al. describe the genomes of several novel Xenorhabdus strain isolated from Kenya, adding to the diversity of this genus and setting the stage for future biotechnological applications. Overall, I agree with the author's conclusions regarding the novelty of these strains, although there are some places where I think that further clarification is needed, especially to avoid overstating what has actually been discovered in this work. Major comments: (1) Several times, the authors describe genes that are unique to each lineage as "causing speciation" (e.g., L. 49, L. 378, L. 507). It is true that gene gain and loss can underpin the creation of species boundaries, although how this works in bacteria is still subject to debate. What is clear is that not all differences in gene content or variation are causal in the speciation process, e.g., much likely accumulates via drift or is genetically linked to causal variants. Because this study only identifies strain-specific variation and does not directly test whether that variation causes speciation, such causal language should be removed throughout the manuscript. (2) The authors repeatedly imply that each Steinernema hosts a unique species of bacterial symbiont (e.g., LL. 79-83; LL. 99-100). However, this is untrue, e.g., the association with X. bovienii with multiple species of Steinernema hosts has been studied in some detail - Murfin et al. 2015 mBio 6:e00076-15, Murfin et al. 2015 BMC Genomics 16:889. That said, those studies did show that there was co-adaptation of X. bovienii strains with the Steinernema hosts from which they had been isolated. Thus, unique variation also exists in Xenorhabdus below the level of species in this case. These nuances should be better reflected in the manuscript. (3) It would be useful to know more about the Steinernema nematodes from which the strains in this study were isolated, if that information is available. Given the introductory material regarding co-adaptation between distinct bacteria-host pairs, it would be especially useful to know if the sampled nematodes represented unique species, especially the hosts for the two X. griffiniae strains. (4) I recommend that the authors moderate the language about defining new species somewhat (e.g., LL. 334-336), given that their analysis is not sufficient to describe new species following the International Code of Nomenclature of Prokaryotes, which would require publication of novel species names in the International Journal of Systematic and Evolutionary Microbiology. I agree that the author's genomic analyses are consistent with BG5 and BMMCB representing currently unnamed species within the genus Xenorhabdus, but this is distinct from and more general than the phrasing used here. (5) Given that the genomes used in the pangenome analysis are draft quality, meaning that they lack certain genes due to assembly artifacts, it seems to me that using 100% presence in all analyzed genomes to define the set of "core" genes is too strict a threshold, even if this is the default used by anvi'o. Instead, I suggest defining the core by using the dendrogram at the center of Figure 2 that clusters gene families by the conservation between the analyzed genomes, which seems to have two main branches that seem to separate conserved and variable genes, even if they are not 100% conserved. Finer nodes might alternatively used, but regardless the issue of how genome quality affects genome content analyses should be explicitly addressed. Similar caveats apply to Figure 3, although this issue seems more difficult to mitigate the with fewer genomes presented here. (6) LL. 358-359: Because two X. griffiniae strains were used in the analysis vs. only a single strain of all other species, it is inappropriate to directly compare the unique genes in each strain to those in the other species. Instead, it would be stronger to compare the genes that are both unique to each X. griffiniae plus those that are shared between the two X. griffiniae strains but absent from all other sampled Xenorhabdus species. (7) The analysis suggesting that gene gain or loss arose to differences in gene content between the four focal strains analyzed here (LL. 380-385) is incomplete and needs to be modified because it does not include a reconstruction of gene content of the common ancestor of the entire BMMCB/BG5/XN45/VH1 clade. This would require discussing the gene content of the phylogenetic neighbors of this clade, i.e., X. bozodoii and the ancestor of X. thuongxuanensis/X. ehlersii/X. ishibashii/X. eapokensis. Methods exist to do this (e.g., ANGST; David and Alm 2011 Nature 469:93) but these were not applied here. (8) I must admit that I have difficulty reconciling the authors' transposon analysis with the BRIG analysis in Figure 4. As I understand it, genomic islands in BG5 are indicated by gaps in the outer two rings, i.e., these genes are lacking in XN45 and VH1. Given the statements about transposons flanking gene islands, I expected the arrows representing transposons to align with those gaps, but they do not consistently do so, i.e., there are many gaps without transposons associated with them and places where the transposons do not obviously align with gaps. Is this because the gaps are relatively small? If most of the gaps are, in fact, not associated with transposons, then I think that this needs to be more explicit in the text, because it implies that transposons are only associated with a minority of genome differences and therefore not the main driver of these differences. Minor comments: (9) Permission for collecting the samples used in this study or that such permission is not necessary must be indicated. (10) Table 1 caption: the genome quality statistics listed in this table are said to be derived from PGAP, but I am unaware of this pipeline performing such an analysis. The methods state that PATRIC was used for this analysis instead, which seems the more likely citation here. (11) LL. 298-300: The terms "monophyletic" and "paraphyletic" are used incorrectly here. "Paraphyletic" refers to the situation where members of two different taxa are interdigitated amongst each other within the same phylogenetic clade. This is not the case here, where BG5 and BMMCB, which are both clearly not X. griffiniae, are clear outgroups to XN45 and VH1, which are; thus, X. griffiniae is monophyletic. All four strains do form a single clade that contains three putative species (contra L. 299 - "BG5 did not form a clade") that would be paraphyletic if BG5 was classified as a different species but BMMCB retained its X. griffiniae classification. However, this paper clearly removes that former classification. (12) Table 2 caption: I suggest adding "of the matrix" to "the top half" and "the bottom half", it took me a while to understand what exactly was going on here. Also, are the ANI and dDDH values given averages of the bidirectional tests? These values sometimes vary slightly based on which genome is used as a query, depending on the implementation. (13) LL. 338-339: "...a pangenome that lacked many strain-specific genes" - I think that "lacked" should actually be "included" here, especially given that the following text describes those genes. (14) As a suggestion, the authors might consider reordering the strains in Figure 2. At the very least, BMMCB and BG5 should be next to XN45 and VH1 because this is the central comparison made in this study. Using an ordering that matches Figure 1 might also make comparisons more logical (i.e., ordering by phylogeny instead of alphabetically). (15) Similarly, I also suggest using the same general order (i.e., from largest to smallest or vice versa) in all of the bar charts in Figure 3b and Supplementary Figure S1 so that they are more directly comparable to each other. Otherwise it gives the impression of differences (largest bars at the top vs. at the bottom) that do not actually exist in the data. (16) L. 466 and L. 470: replace "nascent" with "draft" (17) L. 474: replace "failed to pass conspecific thresholds" with more specific language that describes the actual result, i.e., that the dDDH, ANI, and GGD values were not consistent with these strains belonging to the same species. (18) L. 474: the "sp. nov." designation should only be used when describing a new binomial name, and thus is inappropriate here. It indicates the first use of a species name, not that the strains being analyzed represent a new species that has yet to be formally described with such a name. (19) LL. 497-498: "leads to their overestimation when they occur on contig edges" - is the point here that genes that secondary metabolite genes disproportionately split by contig breaks due to their length and repetitive nature, and therefore have inflated counts? If so this might be stated more explicitly. Miller et al. 2017 Mar. Drugs 15:165 and Klassen and Currie 2012 BMC Genomics 13:14 are both references that make this point explicitly.

    Please rate the manuscript for methodological rigour

    Satisfactory

    Please rate the quality of the presentation and structure of the manuscript

    Satisfactory

    To what extent are the conclusions supported by the data?

    Partially support

    Do you have any concerns of possible image manipulation, plagiarism or any other unethical practices?

    No

    Is there a potential financial or other conflict of interest between yourself and the author(s)?

    No

    If this manuscript involves human and/or animal work, have the subjects been treated in an ethical manner and the authors complied with the appropriate guidelines?

    Yes

  8. Access Microbiology

    Comments to Author

    In this study, the authors isolated new Xenorhabdus strains from nematodes collected from different soils in Kenya. Xenorhabdus species are endosymbiont of Steinernema nematodes which infect and kill insects. The isolation of new Xenorhabdus strains could be of interest to identify new antimicrobials that are produced for this genus of bacteria to eliminate competitors from the soil once the insect is dead. They sequenced, annotated, analysed and compared the genomes of the isolates to classify them phylogenetically and elucidate the pangenome of the Xenorhabdus genus, using for that other Xenorhabdus genomes already published. The pangenome was used to extract the core gene cluster (gene cluster present in all the analysed genomes), accessory gene cluster (present only in some genomes) and strain specific gene cluster (found only in one strain), which were functionally categorizes. The work is well conducted and the results are presented clearly. However, there are some minor issues that should be addressed: Methodological rigour, reproducibility and availability of underlying data 1. In the section of materials and methods "Isolation of nematodes from soils samples", the authors described the use of Galleria mellonella larvae as bait. They should indicate from where they got the Galleria larvae and how they can ensure that the isolated nematodes were not already infecting the larvae. 2. Any Galleria larvae was used or the author selected them within a range of weight. This should be specified in the text. 3. In the section of materials and methods "Isolation of bacteria from nematodes", there are not any reference. How were Xenorhabdus sp. isolated previously? The author should clarify that in this section. Presentation of results 4. There are 27 genomes in the Table S2, which is cited in the text in the section "Creation of pangenomes". However, only 26 genomes (25 species) are used in the construction of the pangenome (Figure 2). 5. In the description of Table S2 is written "…genomes used in phylogenomic and pangenomic analyses". Therefore, Table S2 should be also cited in section "Phylogenomic reconstruction and calculation of ANI values". In this section, is stated that "26 fasta files were used as input…" (Line 215), however, in the Figure 1 there are 27 genomes. 6. Please, clarify the number of genomes used for each section and why X. lircayensis is included in the phylogenomic analyses but not in the pangenome. Any other relevant comments 7. It is difficult to read the page 5 (Introduction, from line 103 to 123) where multiple Steinernema sp. and Xenothabdus isolates are named. I suggest to the authors to include this part in results (supplementary table) and add the Steinernema sp., the corresponding Xenothabdus isolate, if any, the location, and the reference. 8. Line 37 in supplementary Table S2: (Typo) Replace phlyogenomic by phylogenomic.

    Please rate the manuscript for methodological rigour

    Good

    Please rate the quality of the presentation and structure of the manuscript

    Good

    To what extent are the conclusions supported by the data?

    Strongly support

    Do you have any concerns of possible image manipulation, plagiarism or any other unethical practices?

    No

    Is there a potential financial or other conflict of interest between yourself and the author(s)?

    No

    If this manuscript involves human and/or animal work, have the subjects been treated in an ethical manner and the authors complied with the appropriate guidelines?

    Yes

  9. Version published to 10.1099/acmi.0.000531.v1 on Access Microbiology