In this revised version the authors have done several additional analyses and have extensively rewritten the manuscript. The new results strengthen the manuscript and broaden its interest. However, some problems remain about data analysis, especially for polymorphism analysis, which were not performed properly if my understanding is correct. They should be easily corrected but some results may change.

Major comments

• The title of the first paragraph of the results is “…the genome is mostly haploid…”. If the species is triploid due to hybridization it means that two sets of chromosomes should pair whereas the third one should be alone. If I understood correctly, 80% of SNPs were heterozygotes. Does it mean that they correspond to the diploid pair and to the Meselson effect between the two chromosomes?
• The fact that most heterozygotes could be duplicates because of the doubling of the coverage is convincing. But in that case, the two parts of the genome should be split based on coverage. This would allow to analyse separately the haploid and the diploid genome. This would clearly help to better understand the reproductive system of this species.
• The choice of excluding heterozygote sites can be justified so it indeed prevents to compute Fis. However, it would be important to know how behaves the diploid genome. Is there an excess of heterozygotes or not. If not, or it varies along the genome it could be informative of the kind of asexuality. Modification of meiosis could also be a possibility instead of mitotic reproduction (for example see (Lenormand et al., 2016, Engelstadter, 2017)). We could imagine a form of automixis with one set of haploid chromosome transmitted as a block without segregation.
• Related to this important question, and still if my understanding is correct, it’s important to note that the lack of recombination is shown (nicely, see below) for the haploid genome (which is expected) but not for the diploid genome. Absence of recombination for the diploid genome (+ Fis <0) would be a strong argument for mitotic recombination (but still some for of automixis can lead to a similar pattern)..
• If I understood correctly, SNPs are defined as variant compared to the reference. Then polymorphism is computed for each strain as the % of SNP. But this is not a measure of polymorphism of a strain but of the genetic distance between the strain and the reference. If only homozygote variants are kept, piS and piN cannot be computed for a strain. Here what should be done is to compute piS and piN for the whole species and also interestingly for the three clusters detected by the PCA. And when computing these statistics the reference genome should not be considered, except if the reference strain is added as a data point.
• If the order of magnitude of piS and piN/piS is still valid after correction, it is interesting to note that, although piN/piS is three times higher than in outcrossing nematodes, it is still lower than many other species, including human (around 0.2).
• The PCA and phylogenetic tree do not support clustering by host. This could be used as an opportunity to try to identify the few SNPs (if any) that could be associated with hosts. It is not possible for all host but for those that can be found in different clusters such as soybean, cotton and tobacco.

Minor comments - The test of absence of recombination is a nice addition and the idea of comparing to a recombining species is a nice control. This part could be move earlier (second or third part of results for example). - It was not one of my previous comments but I’m not really convinced by the argument stating that an ancient polyphageous strain is not very likely. Here the number of strains is too low for ancestral state reconstruction. I don’t mean that this idea is wrong but that the alternative proposed by the other reviewer could also be discussed and that additional data would be needed to test it properly.

References: - Engelstadter, J. 2017. Asexual but Not Clonal: Evolutionary Processes in Automictic Populations. Genetics. - Lenormand, T., Engelstadter, J., Johnston, S. E., Wijnker, E. & Haag, C. R. 2016. Evolutionary mysteries in meiosis. Philos Trans R Soc Lond B Biol Sci 371.

In this manuscript, the authors collected 11 ‘isolates’ of the parasitic root knot nematode Meloidogyne incognita from 6 different crops. These isolates were then assigned to four ‘host races’ traditionally recognized in the species based on the ability of nematodes to infect particular reference crop species (these reference species differ from the crops the nematodes were collected from). The authors then re-sequenced the genomes of the isolates and inferred SNPs relative to an available reference genome of the species. Two independent clustering approaches based on the SNP data (PCA and a phylogenetic network bases on the subset of SNPs in coding regions) indicate that the 11 isolates form 3 diverged clusters. From these clusters the authors draw the following 3 conclusions:

1. The clusters do not correspond to ‘host races’ and the use of the term ‘host race’ should be abandoned for M. incognita. I have no problem with this conclusion - in more ‘standard’ terminology, host races are polyphyletic and correspond to a phenotype rather than a lineage. However, the authors also state that these data indicate multiple independent adaptations to different host ranges. In the absence of information of ancestral host ranges, this is clearly an over-interpretation. For example, one could imagine a highly polyphagous ancestral lineage (i.e., with extreme phenotypic plasticity for host plant use), but the ability to infect specific hosts was lost independently in different lineages. The title “Parallel adaptations to different host plants despite clonal reproduction in the world most devastating nematode pest” should therefore be abandoned as it does not reflect the findings of the paper.

2. The authors state that there is no correlation between the diverged clusters and the geographic origin of the samples. However, according to Fig 5 this is not entirely true as there is some clustering of geographically close samples. Instead of eyeballing whether or not the genetic clusters correspond some grouping of samples from a given country, I suggest the author conduct standard IBD analyses and calculate the % of genetic variance explained by geographic distance (i.e., using pairwise geographic distances between isolates). This % will be small, but represents a more objective evaluation of the effect of geography.

3. Similar to point 2, the authors also state that there is no correlation between the clusters and the crop species where the isolates were collected. This is difficult to evaluate given the small number of isolates (n=11) relative to the number of crops (n=6). Nevertheless, 3 of the 4 isolates from cotton are members of the same cluster, as are the 2 out of 2 isolates from tobacco, so there appears to be some correlation. Again, I suggest that the authors quantify the amount divergence of isolates of the same vs different crop species to show that the amount of variance between crops is not larger than the variance within.

Finally, there are parts in the methods that should be clarified. For example, I believe the term ‘isolate’ usually refers to a strain derived from a single female, but here apparently it is a pool of individuals collected at a given location (or even from multiple locations for isolate R3-4, see line 117). How did the authors deal with population variation – was only the major allele considered at each position? Along the same lines: M. incognita is a hybrid species and highly heterozygous. I believe the reference assembly is largely haploid (the two parental genomes are assembled separately), meaning there will be no heterozygous positions for a genome based on a single genotype. These points do not affect the results but should be clarified in the methods.

Minor comments. - In the discussion of divergence from the reference genome for nuclear and mitochondrial sequences (L241 and following), I am surprised the authors are not mentioning lack of recombination – the lack of recombination in mt genomes contributes to their relatively high substitution rates in comparison to the nuclear genome in sexual species. This difference no longer exists in M. incognita. -L134, 135: do you mean divergence from the Morelos reference strain? (are these uncorrected p-distances?) -The map in Figure 1 has 13 isolates listed for Brasil, not 11. -L108: I dont understand the sentence “Considering the clonal reproduction of this species, the route of adaptation to different hosts is evolutionary important since it is unknown whether it happens independently or a consequence of four ancestral states.” -‘Host preference’ usually refers to a neurological mechanism of preferring one host over another, not to being able to infect one host but not another. I would chose a different term.

This manuscript presents a survey of genetic diversity at the whole genome level in the root-knot nematode Meloidogyne incognita, which is a clonal worldwide plant pathogen with different host races. The main question was to determine whether these races corresponded to distinct genetic clusters. Three main genetic clusters were found but they are neither associated with host races nor geographical origins. This result is interesting with important practical implications and the ms clearly presents this main result. However, I think that the dataset (whole genome sequence of 11 strains + additional published genomes) is clearly under-analysed and that a better knowledge of the system could be reach, also with potential practical implications. This version should be sufficient for a specific audience specifically interested in the biological model. But to reach a broader audience, additional analyses should be done

MAJOR COMMENTS

A major assumption is that the species is clonal. However this is not discussed while the data could help to evaluate more precisely the breeding system of the species. Is the species really completely clonal? Is it recent or not? For example, Fig 4 represents a network and not a fully resolved tree. In a purely clonal species, a perfect tree should be expected. Potential signature of genetic exchanges could be assessed with the current dataset: - Under pure clonality all genomic regions should give the same history. So first did you get the same nuclear and mitochondrial tree? Then, if you split the nuclear dataset into blocks (chromosomes or shorter blocks) do you obtain the same tree for all blocks? This is a simple way to test whether genetic exchanges have occurred or not? - There are also different methods to test the occurrence of recombination (or gene conversion) that should be applied here (ex: decrease of linkage-disequilibrium with distance, four-gamete test, and more elaborated methods) - Individual heterozygosity is not given. Under pure clonality, excess of heterozygosity (Fis <0) is also expected I think this point is crucial to correctly interpret the results.

Genetic diversity is only briefly analysed and not very precisely. P6 l133: What is exactly “level of variation”? Does it mean Tajima’s pi or another statistics? To allow comparison with other species it would be interesting to compute pi synonymous (or 4-fold): is it of the same order of other clonal or selfing species? The comparison with selfing and outcrossing nematodes should be particularly relevant. More generally, recent surveys of genetic diversity can be used for comparison, for ex: - Romiguier et al. 2014. Comparative population genomics in animals uncovers the determinants of genetic diversity. Nature 515:261-263. - Chen, J. et al. 2017. Genetic Diversity and the Efficacy of Purifying Selection across Plant and Animal Species. Mol Biol Evol 34:1417-1428. To better interpret piS in term of effective population size (Ne), an idea of the mutation rate should be important also. In addition to piS, the piN/piS ratio should also be computed and given. It gives an idea of the efficiency of selection and is usually rather well correlated with Ne. This could be compared also with previous studies.

The analyses suggested above could be done at the whole species level but also for the three different genetic clusters separately. In addition, Fst should be given to get a more quantitative idea of population structure than just the PCA.

It would also be interesting to present the distribution of genetic diversity along chromosomes. This could also bring information about potential rare or past recombination events, for example if there is more genetic diversity in telomeric than in centromeric regions.

“M. incognita is particularly versatile and adaptive despite its clonal mode of reproduction”: this interpretation implicitly assumed that adaptation to the host is highly multigenic and complex. However, if only a few key genes determine host compatibility, the problem of being clonal is much less important and it maybe not necessary to invoke CNV or epigenetic mechanisms. It would also explain why there is no association between genetic cluster and host race.

Because there is no association between genetic cluster and host races it is potentially a good situation to identify genes potentially involved in adaptation to the different hosts. The sample size may be too small but more elaborate genomic scan could be done rather than simply searching for specific SNPs. In particular, the genomic location should be taken into account to increase the power of detection.

MINOR COMMENTS

P4 l73: “no clear genetic differences underlying the phenotypic plasticity” this is not well formulated because strictly speaking phenotypic plasticity does not require genetic variation, otherwise we would rather use “local adaptation”

P5 l96: “in this analysis; no relation” --> “;” should be replaced by “,”

Fig 2: Number of variants per isolate: to what are variants defined? The reference strain?

Fig4: the scale on the figure is too small and hardly readable. Is it 0.1?