Peer review of: Exceptional subgenome stability and functional divergence in the allotetraploid Ethiopian (2020)

Reviewers' comments: 

Reviewer #1 (Remarks to the Author): 

In this paper VanBuren et al present and describe a new genome assembly for the polyploid species 
Eragrostis teff. This chromosome scale genome assembly is based on PacBio reads along with HiC data 
and represents a great improvement in comparison to the previously available illumina based draft 
assembly (Cannarozzi et al, 2014). Indeed the statistics of completeness and contiguity for this 
assembly are impressive. Furthermore, using genome counterpart specific repetitive sequences the 
authors were able to associate each chromosome to the original donor genome (A or B). Analyzing the 
insertion time of TEs and their genome specificity the Authors were also able to estimate that the 
polyploidization event took place ~1.1 MYA. Analyzing the Ks between homeologus genes in E. tef the 
authors estimated that the two donor subgenomes diverged ~5.0 MYA. No major genome 
rearrangements were detected indicating an exceptional genome stability. Authors then provided an 
extensive survey of tef transcriptome showing divergent expression patterns among homeologous 
gene pairs. 
Definitely this is a great resource for those interested in tef and more generally in orphan crops. Also 
it is a nice piece of work providing interesting insights in polyploid genome structure and functioning. 
Nevertheless there are few issues and a certain lack of detail that should be addressed by authors. 
-First I would like to have the general statistics regarding repeats and TEs content and distribution 
moved to the main text (at present these data are provided in Supplemental Table 3). Indeed, as it 
clearly appears from the methods section, TEs annotation was carried out thoroughly but no general 
data are presented. Just a simple table clearly stating the amount of LTR-RT (possibly detailed for 
Ty1-copia and Ty3-gypsy), LINEs, SINEs etc… would be useful. I know that most part of this 
information is in main text and in supplemental data but I think that having it also in a single table in 
main manuscript would be beneficial for the readers. 
-Then always related to TEs and in particular to those families seemingly specific for genome donors, 
all the period going from “We classified...” to “Supplemental table 5” (lines 177-192) is confusing and 
should be better described since it has a pivotal role in this manuscript. More in detail, it seems to me 
that authors dated the polyploidization event at 1.1 MYA (or before) basically relying on two facts: 1) 
all the species specific families (six) should have amplified before polyploidization and 2) the 
estimated insertion time is > 1.1 MYA for all the elements belonging to these families. I do not know if 
I got the reasoning correctly here. If not please apologize and explain. Anyway if this is correct then 
there is another simple test that authors should carry out to further support their conclusion. Consider 
out of the “24 families with median insertion times between 1.1 and 2.4 MYA” those that “do not 
exhibit subgenomic specificity”. In this case, if you build a phylogenetic tree separately for 
PostPplyploidization (IT < 1.1 MYA) and PrePolyploidization (IT > 1.1 MYA) inserted elements then, for 
the first group elements should mix up whereas for the second subset they should separate in two 
distinct clades. Some families that could be considered for this exercise are 4, 6, 15, 16, 17, 25, 41, 
43, 45, 52, 60 and 61. 
Authors then stated that “The insertion times for these genome-specific LTR-RTs were all greater than 
1.1 mya, indicating the two subgenomes were evolving independently during this period” but this 
doesn’t seem to be the case of Family 14 that shows evidence of recent activity (supplemental figure 
4). 
Also authors concluded that because “Five of the six subgenome-specific LTR-RT families were found 
only in the A subgenome” then “LTR-RTs accumulate more rapidly in the A subgenome or are purged 
more effectively in the B subgenome.” I am not completely sure about this. These are just subfamilies 
and authors are using their distribution pattern to infer the activity for the whole set of familyes: 65. 
Other more specific points to fix or clarify are: 

Line 84: is there a particular reason for focusing on “Dabbi” cv.? If there is, briefly explain it. 
Lines 91-92: Authors should better specify the evolutionary relationship between E. tef and Oropetium 
thomaemum. How close is “closely related”? 
Lines 99-102: from “ Illumina reads from...” to “...between homoeologous regions”. All this part 

should be moved to Materials and Methods 
Lines 115-117: It doesn’t seem that the incongruences in figure Figure 2, chr 8A are negligible. Quite 
likely they could be explained somehow... but “negligible” seems to me an understatement. 
Lines 142-144: These satellite sequences could well be centromeric satellite sequences. However it is 
important to be aware that the definition of centromeric sequence could not be based only on length 
and tandem arrangement. Here no prove is provided regarding the actual localization (FISH) and 
function (ad hoc biochemical essay) of these sequences although the analysis of co occurrence with 
centromeric specific Ty3-gypsy elements is a reasonable proxy. For these reasons I think that these 
sequences are for sure satellite sequences but they are only putatively located in centromeres. 
Because of this I would suggest to change CentT in SatT. 
Lines 148-149: “This element was previously identified in the draft teff genome”. Actually it was not 
identified in the draft teff sequence but in a set of random sheared MiSeq reads collected from a third 
Teff variety: Enantite 
Line 158: “The Teff subgenomes have 93.9% sequence homology”. It is not “93.9% homology” but 
“93.9% similarity”. Homology by definition means: “sharing a common ancestor” and so it can not be 
quantified as a percentage. It is there or it is not. 
Lines 163-164: mention the mutation rate here (not just the reference) 
Line 166: Table 1. In this table it would be nice to have listed also the TEs content for each 
chromosome. 
Lines 177-178: “We classified LTRs into families” please explicit that these families are 65. 
Line 202: “Teff and Oropetium show a clear 1:2 synteny pattern” Shouldn’t it be the opposite, i.e. a 
2:1 pattern? 
Lines 217-221. Supplemental table 6. Why 0.38 was chose as cutoff? Also list in supplemental table 6 
the actual Ka/Ks values as well as, if available, the associated probability 
Line 222: “These genes may have been intentional or inadvertent targets during domestication.” 
Based on the presented data this is pure speculation and authors shouldn’t build a case on these very 
limited data. My suggestion is to remove this sentence. 
Lines 230-231: ”The A and B subgenomes of teff have a near identical number of syntenic orthologs to 
Oropetium (19,277 vs. 19,292 respectively)”. Are they also mostly the same genes? 
Lines 232-233: “Orthologs to 1,308 Oropetium genes are found as single copy loci in teff, including 
647 and 678 from the A and B subgenomes respectively”. They Do not sum up to 1308 but 1325 
Line 278: “homoeologous expression bias” Use HEB instead to be consistent. 
Line 314: How much distant is “distant related”? Please put here some estimate of the divergence 
time between the two species. 
Line 319: “Ph1-equivalent locus (loci)”. Briefly explain. 
Lines 360-369: It would be useful to add a supplemental figure clarifying the experimental design 
Line 399: why a unimodal distribution does indicate high differentiation between the two subgenomes? 
I would have expected the opposite… 
Line 416. Typo: “previuously” → “previously” 
Lines 449-450: This has already been said in results, so it is redundant. 
Line 473: specify the reference for the ratio you used. 
Line 482. Why did authors use such an old version? This is just out of curiosity. With newest version 
result shouldn’t change, though. 
Lines 517-519: any estimate of the amount of genes excluded because of translocation? 

Reviewer #2 (Remarks to the Author): 

VanBuren and colleagues have produced a high-quality assembly and annotation of the polyploid and 
orphan crop, Teff. The data produced and basic analyses related to genome construction are of the 

highest quality. However, I have a number of questions and concerns about the analysis and 
interpretation; these are detailed below. 

Major comments: 

1 … The title and take-home message of the manuscript regard excessive subgenome stability in Teff. 
The term exceptional implies that genomes of other species are far less stable. Despite detailed results 
of gene expression, large-scale collinearity, sequence similarity and TEs within Teff, there are few 
comparisons to the distribution of these parameters in other polyploids — so the reader is left to figure 
out on their own how exceptional Teff really is. For example, I’m not sure of what to make of the term 
‘high degrees of’ synteny (line 313), since there are no baselines provided to compare to. Where 
examples are provided (e.g. Edger et al. 2017, line 329) the comparisons are limited to one or a few 
papers and not of comparably ancient polyploids. 

2 … Lines 125 – 138 and 223 - 235: Using annotated sequences as a proxy for presence absence 
might be error prone – annotations are thresholded based on a variety of scores, so the presence of a 
gene but not its homeolog might be just as likely to be due to real sequence divergence as 
thresholding based on homology or expression support. Are you invoking pseudogenization as the 
primary mechanism here? If so, perhaps adding an analysis of the presence / absence of modeled 
pseudogenes or low-support gene models would help. 

3 … Line 211 and elsewhere – what is meant by ortholog? Can’t find mention in the methods about 
orthology inference. Just sequence similarity via last. Also, what is meant by syntenic? Just that the 
genes are in an mcscan block? If so, are all points in Fig. 4C considered syntenic? If so, what do you 
make of the apparent duplications (e.g. 1A/B(teff):6(oropetium)). 

4 … I'd like to see more detail about how differential expression analyses were accomplished. Some 
things that should be addressed: 1) what statistical test, level of replication and software was used to 
determine HEB? — I think this is a test of allele-specific expression in 1:1 homeologs, but I am not 
sure how it was actually conducted. 2) How were genes with non-unique mapping handled? That is, 
were reads that mapped to both homeologs discarded (which might increase your ability to find HEB, 
and thus type1 error) or were they both counted? If the annotation was split into subgenomes before 
analysis, it might be worth exploring more nuanced allele-specific expression software like EMASE. 3) 
Its not clear how a wilcoxon test would be applied here – there is pseudo-replication at the level of 
homeolog among 207k non-unique comparisons (each gene is tested 10x). 4) How were multiple tests 
corrected for? It appears that 207k tests were made, but I imagine that FDR corrections were only 
employed within tissue type/treatment. Please detail how experiment-wise FDR was controlled. 

-- 
Minor: 

I don’t understand the hypothesis explored in lines 257-259. Wouldn’t homeologous exchange simply 
lead to multi-mapping reads (or identical expression if subgenomes mapped independently) and 
therefore not appear in HEB? 

Historical patterns of selection are inferred both as sequence variation during domestication and in 
reference to HEB. These are accomplished without a lot of possible corrections for demography etc. I’d 
say these sections (lines 217:222, 286-291) could either be significantly bolstered by more nuanced 
analyses or presented as hypotheses. Plus, lines 217-222 don’t really fit with the results having to do 
with subgenome differentiation that surround it. 

I would disagree Fig 4C shows that teff and oropetium have near complete collinearity (Line 200). To 
me, this shows lots of inversions, translocations, etc. Furthermore, in the next sentence, it is stated 
that 13-15% of all genes do not display expected patterns of collinearity. 

Since the article is about subgenome stability, I’d like to hear more about why copy number in arrays 
vary so extensively (Line 171) … more than other polyploid grasses with similar ages? 

I was interested in the different sizes of the subgenomes, a fact is mentioned several times 
throughout; however, a quantification of the factors that lead to larger A subgenome is not 
accomplished, just general statements like that of line 189. 

This is personal preference, but I found the genome assembly and annotation sections to be mostly 
methods with some summary statistics. To me, this is best summarized in a few sentences in the main 
text and expanded in the supplement (and methods), since these results do not address the central 
theme of the manuscript. 

Reviewer #3 (Remarks to the Author): 

Robert and co-authors sequenced the genome of allotetraploid teff, a type of cereal crop in Africa, 
through the combination of SMRT long reads and HiC data. They further separated the two 
subgenomes in the teff genome, and observed the homeoelog expression dominance between the two 
subgenomes. I have some suggestions for the authors to improve the manuscript before further 
consideration. 

1. In the introduction section, it is introduced that the teff has “desirable nutritional profiles, abiotic 
and biotic stress resilience, and untapped genetic potential”, and is “among the most resilient cereals, 
tolerating marginal and semi-arid soils”. However, no such evidences have been provided in the 
analysis of the genome. The current manuscript lacks of biology research contents. Please focused on 
two or more biology features of teff, such as “nutritional profile” or “tolerating marginal and semi-arid 
soils”, providing the genomic evidences and the underling biology stories. 
2. The manuscript only focused on the genome sequencing, subgenome partition and homoeologs 
expression differentiation, while the evolution of the species to other cereal or close related species 
has not been provided. I suggest the authors to add these contents, such as phylogenetic tree, ka/ks 
among species, etc. 
3. Authors discussed that the diploid ancestor of the teff might be extinct. However, no such analysis 
has been performed, authors should provide the evidence of the closest genomes to the two diploid 
ancestors, which may provide clues to trace the diploid ancestor of teff. 
4. The authors discussed it that “wild progenitor of teff is likely Eragrostis pilosa”, please provide some 
genomic evidences. Furthermore, the teff cultivar “Tsedey” was annotated to have 50006 genes, while 
the assembled teff has predicted 68,255 gene models. Why they are so different in gene numbers, 
what have been expanded, and how to evaluate the accuracy of the gene prediction process? 
5. For the subgenome specific LTRs, they are very small in numbers, author identified 8-23 LTR copies 
for the six subgenome specific LTRs families. Please provide the statistic tests for such number of 
insertions occurred by random events. 
6. The title name “Subgenome origins” should be changed to something like “subgenome partition…”, 
since the origin of the two subgenomes has not been analyzed. 
7. In lines 110, please explain why there are 32 linkage groups obtained from the population, which is 
much more than the number of chromosomes? How can you use this information and will not 
introduce extra errors? 
8. Have the authors estimated the heterozygosity of the sequenced material, and how is the 
heterozygosity? Please provide this parameters. 
9. In the abstract, “The exceptional subgenome stability” should not be the reason of “diversification 
of these grasses”.