Peer review of: Recent hybrids recapitulate ancient hybrid outcomes (2019)

Reviewers' comments: 

Reviewer #1 (Remarks to the Author): 

The paper addresses an important and interesting question, comparing an older hybrid zone with 
contemporary hybridization. Overall, I think this is a great study that will be broadly interesting, the 
analyses are thorough, and the paper is very well written. I think the authors did an excellent job of 
distilling very complex analyses into a concise manuscript. I am very excited about this paper and I 
enjoyed reading it, but I do have concerns about how some of the results are interpreted. 

The introduction and discussion only considered selection as a mechanism for consistent genomic 
patterns between ancient and recent hybrids. I think ignoring the recent literature on the role of 
recombination, gene density, and other structural features on patterns of divergence and shared 
ancestry is major omission. Structural features of the genome can also lead to shared ancestry tracks, 
for instance introgressed segments can persist in regions of the genome where there is low 
recombination. The authors do allude to this on Lines 298 and 299, but I think this is relevant to the 
discussion about the Jackson Hole/Dubois populations as well. 

I don’t think “ancient” is the right word for the Jackson Hole hybrids. Generally, the term ancient 
hybridization is used for cases where hybridization is found between allopatric taxa or taxa where one 
lineage is extinct. What is the evidence that there is no recent hybridization in Jackson Hole or that 
the Jackson Hole hybrid populations have progressed towards genome stabilization? I agree that the 
analyses here suggest the Dubois population is more recent admixture than other Jackson sampling 
sites and I think the comparisons of these populations is fundamentally interesting. But to me, 
admixture in the Jackson Hole populations is more consistent with adjacent/intermixed populations 
that experience periods of contact and backcrossing in a patchy environment (Gompert et al. 2010), 
rather than an ancient stabilized hybrid lineage. 

As it is currently presented, the discussion and presentation of the admixture results is a bit 
misleading. Fig 1 shows an idealized version of hybrid indices for an ancient hybrid lineage and recent 
hybridization, but only the hybrid indices of Dubois population (recent hybridization) are presented in 
the main text (e.g. Fig 3A). The distribution of hybrid indices for Jackson Hole is presented in a slightly 
different format in Fig S1, but does not match the predictions of ancient hybrid lineage presented in 
Fig 1. Jackson Hole hybrids have hybrid indices close to L. idas, with evidence of admixture up to 
~0.20 from L. melissa, which I would interpret as backcrossing of rare hybrids into L. idas, with little 
gene flow from L. idas allopatric populations. Indeed, in a prior study the ancestry of Jackson Hole 
populations was so close to L. idas, that there was no evidence of admixture using treemix and 
structure plots generally showed the same patterns between L. idas and Jackson Hole, with slightly 
more L. melissa ancestry in Jackson Hole (Gompert et al. 2014, Figs 4, 5, 6). The relative amount of 
admixture for Jackson Hole populations are not that different from the admixture in what is defined as 
pure L. melissa populations (Fig S1, this manuscript). I think all of this could be made clearer is some 
version of Fig S1 were included in the main manuscript. 

I think the description of the results of the PCA is also a bit misleading. There is not a clear distinction 
between Jackson Hole hybrids and L. idas. There are L. idas individuals clustered with Jackson Hole, 
and vice versa. While there are variants that distinguish these overall populations, the same pattern 
can be seen in modern humans or any other species that has population structure and isolation by 
distance. Given the past interpretations of the patchy population structure of these sampling sites, the 
manuscript should include explicit measures of IBD. Finally, while I agree it is likely that the Dubois 
population is a product of hybridization between L. melissa and Jackson Hole (based on the location of 
the sites), I don’t see how that can be firmly established given that there are both Jackson Hole and L. 
idas individuals clustering with some Dubois individuals in the PCA? Are there additional analyses that 
support this? Overall, I think the manuscript should be more cautious in interpreting the PCA. 

All that being said, I think this is a matter of presentation and I don’t think that being more cautious 
in the interpretations would decrease the impact or the appeal of the manuscript. Regardless of how 
the Jackson Hole hybrids are described, it is still a very interesting and exciting study to compare 
ancestry in these hybrids relative to new Dubois populations. 

Minor comments: 

I think the patterns of consistently restricted introgression on the Z chromosome is indeed interesting, 
though it isn’t particularly exceptional (Line 300). The discussion of factors underlying restricted Z 
introgression should also mention linkage (modeled in Muirhead and Presgraves, The American 
Naturalist, 2016). 

Line 52: “genome collisions” is a bit much (also Line 86, 314). 

Line 78: citation? 

Line 102: The cluster for Jackson Hole is not particularly tight, and if other populations of Lycaeides 
were included in the PCA, then Jackson Hole populations cluster with L. idas, as presented in Gompert 
et al. 2014 (Fig 1B). 

Fig 1C: Maybe indicate that this is the hypothesized relationship among these populations? 

Fig 2: The populations on the map could be related to the PCA through either a gradient of colors or 
shapes. The shapes/colors could also correspond to the PC scores in Fig 2C. Color blind readers can’t 
distinguish this color palette, and especially in this figure, would miss critical information. The colors 
should be changed. 

Fig 5 is an excellent summary of results, but it could be easier to read if it were a bit bigger, especially 
the text? 

Fig S2: If this is mean LD shouldn’t there be standard deviation or error estimates? Maybe I am 
misunderstanding how mean LD is calculated. 

Line 239-242: It is exciting to see a cold tolerance/diapause gene in the list of candidates, especially 
given the difference in diapause between these two species. 

Line 306-310: It could be said that any study of speciation links macro and microevolutionary 
processes (in fact, that is how I define the study of speciation), and to be fair many studies make 
those links much more explicitly than this study, and in a comparative phylogenetic framework. I think 
this is overselling. 

Line 410: typo? “to gene model” 

Line 414: ‘partial genome sequences’ sounds like whole genome data. It might be clearer to identify 
these data as GBS. (also on Line 79) 

Reviewer #2 (Remarks to the Author): 

Chaturvedi et al. studied the genomic composition of hybrid-origin lineages of Lycaeides butterflies 
using a large dataset and a newly-assembled genome. Hybridization provides an exceptional 
opportunity to study the impacts of selection on the genome and its role in the origin of species. The 
study system and dataset used here are well suited to address these questions. The main finding of 

this study is that genomic regions showing extreme ancestry of one or the other parental species in an 
older (Jackson Hole) hybrid lineage show significant overlap with those showing non-neutral patterns 
of ancestry (either excess introgression or barrier-like patterns) in a younger (Dubois) hybrid lineage. 
This highlights an important role for selection in speciation. 

Overall I think this is a well-conducted study and a well written paper with results of broad interest. 
Most of my concerns are about providing more information and interpretation to improve clarity. 

1. Developing expectations 
The major obstacle for me in getting my head around this study is the fact that the two main focal 
lineages, Jackson Hole (JH) and Dubois (DBS), are not independent realizations of distinct 
hybridization events. Rather, the former lineage is thought to be a progenitor of the latter (line 77). 
While the non-independence is not a fundamental problem, it does alter our expectations. For example 
in Figure 1, we see how the genomes of ancient hybrids might have largely stabilized, whereas those 
of contemporary hybrids can be variable, but if we place this example in the context of the present 
study, and assume that blue represents L. melissa ancestry and gray represents L. idas ancestry, then 
the combination of ancestral and contemporary hybrids shown in Figure 1 would not be possible in the 
case of JH and DBS: the contemporary hybrids have idas ancestry in parts of their genomes where 
neither of their parental lineages (JH and melissa) could have contributed it. My point here is not 
about this schematic figure per se, but that the nuances of this situation need to be better laid out for 
the reader in the text early on. For example, in parts of the genome where JH is fixed for melissa 
ancestry do we even expect to be able to distinguish JH and melissa ancestry in the DBS population? 
(See my next point). 

I also found the order of the first two results sections a bit odd. It is difficult to interpret the clines in 
the DBS population without first understanding the composition of JH. For example, reading that only 
10.9 and 3.5% of the genome of JH is fixed for ancestry of each parental species did change my view 
of the whole story (again, perhaps Figure 1 is a bit misleading here). I also thought that before seeing 
Figure S6 it would be useful to see an equivalent figure showing how JH frequencies compare to those 
in its parental populations. Unless there is good reason not to, I suggest the authors consider placing 
the section on JH ancestry first in the results. 

2. AIMs for JH 
The Ancestry Informative Markers used for bgc in DBS are said to be defined based on frequencies in 
idas and melissa (line 123), but they have (understandably) been applied using JH as a reference 
population. Given that JH is itself partly of melissa origin, do these AIMs provide sufficient power to 
distinguish JH and melissa ancestry in DBS in all parts of the genome? For example if there is less 
melissa ancestry on the Z than on autosomes in JH, then perhaps there is also more power on the Z to 
detect JH ancestry in DBS. If so, is the finding of greater JH introgression on Z in DBS still valid? 

My above concern was somewhat alleviated when I later saw that AIMs in regions of excess melissa 
ancestry in JH also show evidence of excess introgression in DBS, but as noted above, I am puzzled 
about how it is possible to distinguish melissa and JH ancestry in such regions. I expect this apparent 
paradox and its potential implications for systematic biases will concern other readers too, so it should 
be directly addressed in the text. 

3. Introgression from JH 
Again related to the above - of the three significant overlaps in Figure 6, I was surprised by the 
overlap between AIMs showing evidence of introgression into DBS and regions of extreme melissa 
ancestry in JH. Since DBS received melissa-like variation from both parental species, why should the 
JH alleles introgress and replace those from melissa? 

4. Overlaps 
Is there a reason that AIMs showing evidence of introgression (positive alpha) are compared 

separately to regions that show either excess idas or melissa ancestry in JH, whereas AIMs showing 
barrier like patterns (positive beta) are compared with a combined ‘extreme’ category? 

5. Reduced introgression between melissa and Warner mountains on the Z 
Line 292 implies that reduced occurrence of trees clustering melissa and the Warner lineage on the Z 
is indicative of reduced introgression. In order to account for the confounding effect of Ne on lineage 
sorting, this needs to be compared to the abundance of other types of non-species trees, in particular 
the tree grouping Warner with idas. Alternatively the ABBA-BABA test and related f estimators control 
for this confounding effect. 

6. Effect of chromosome length? 
Visually, the phylogenetic results appear to agree with the finding of Martin et al. (2019 PLOS Biol) 
that introgression is generally reduced on longer chromosomes. Can this be tested? As noted above, 
the distinction between differences in rates of lineage sorting and differences caused by reduced 
introgression is a key consideration here, and discussed at length in the Martin et al study. 

Minor comments 

7. In line 109, I think it is worth noting that the elevated LD in DBS is positive or coupling LD, and 
therefore informative about ancestry. 

8. An additional statement in the results addressing directly why two different methods (genomic 
clines for DBS and ancestry tract analysis for JH) were used, would be useful. 

9. Can distinct symbols be used to distinguish the different JH populations in the map and PCA (either 
in Figure 2 or a supplementary figure)? It is impossible to fully relate the PCA to the map, and also to 
Figures 2C and S1 without this information. 

10. The argument that autocorrelation in window-based phylogenies is more consistent with 
introgression than ILS (line 286) needs to be expanded a bit for the non-expert reader. 

11. Please use the same y-axis scale for Figures 6F, G and H. 

12. Trees 1:15 in the phylogenetic analysis should all shown somewhere. 

13. I recommend adding further discussion of the implications of these findings for the relative 
importance of extrinsic and intrinsic barriers in speciation. 

Simon Martin 

Reviewer #3 (Remarks to the Author): 

Chaturvedi et al. reported genomic regions that are likely involved in reproductive isolation (“barrier 
loci”) and selection by using a newly discovered hybrid zone and two ancient hybrid populations of 
Lycaeides butterflies. Using a contemporary hybrid zone and comparing it with ancient hybrid 
population/species is very unique and provides new insights into how same genomic regions can be 
involved in reproductive isolation. The Helianthus sunflower is one of the pioneering systems to 
investigate such a pattern, but unfortunately, reproductive isolation between the parental species is so 
strong that it is not possible to investigate the pattern reported in this study. 

I do not have much to suggest to further improve the manuscript, but one thing that I am missing is a 
relationship between the putative barrier loci and chromosomal rearrangements. For instance, 

inversions have been known to be associated with barrier loci by suppressing recombination. Dovetail 
recently released “Omni-C”, which may provide chromosome-level assemblies for whole genome 
phylogenomics analysis (Line 602) to investigate structural differences between species/populations. 
Since structural reorganization of genomes appears to be common in butterflies 
(https://advances.sciencemag.org/content/5/6/eaau3648) and many other species, it is tempting to 
speculate such a scenario in the Lycaeides system. Perhaps 1-2 lines of discussion about this may be 
worthwhile. 

Specific comments: 
Line 110: Figure S4 uses all markers (ie., not only AIM). 

Line 197: Figure 5D -> 5F. Also please check the values (35.42 in 1% stringency, which looks like 
~40% in Figure 5F) 

Line 606-: I could not find summary statistics about “high-coverage”. Please state DP/variant or 
genome-wide read depth. 

Figure S5: Mean minor allele frequency of 1164 AIM?