Peer review of: Transition to naïve human pluripotency mirrors pan-cancer DNA hypermethylation (2020)


 
 

Reviewers' Comments: 
 
Reviewer #1: 
Remarks to the Author: 
The authors have addressed various questions raised in response to the 1st submission. Some of 
the remaining concerns are listed below which can be addressed through discussions in the paper 
and figure edits where required. Barring these changes, the paper looks good for publication and 
brings forth novel findings and concepts. 
 
1) The studies with DNMT3A/B KO and HOX gene 5mc/hmc studies lead to inconclusive results 
regarding the functional impact of hypermethylation. This is suggested in the rebuttal letter and 
could be discussed in the paper for the sake of proper context for interpreting and clarity to the 
reader. 
 
2) The dynamic nature of the methylation, i.e. hypermethyaltion in late-transition followed by 
demethylation back to almost the primed-state levels should be enhanced further in the 
discussion/stated in the abstract. Because the current text conveys the message that the 
“reprogramming” ends up in a final hypermethylated state which is not the case. An accurate 
description in the abstract should read: TRANSITION to “naïve pluripotency and oncogenic 
transformation share common…” (Abstract). This is indeed an interesting finding in this model 
although the functions are not easily discernible. 
 
3) Some figures regarding KD studies show only primed and late but not early, naive, and various 
combinations thereof (example Suppl. Fig. 5). Since it s a progression model, it is more useful to 
know the impact of the manipulation throughout the progression stages. For example, in Suppl. 5b 
(“qRT-PCR for the transcripts of the DNMT3 family in control and knock-down cell lines, across the 
period of resetting.”), the data only shows primed and early and not “across the period of 
resetting”. Important to carefully present this because in Fig. 3a and b “DNMT3A is not solely 
accountable for all the hypermethylation present”. Was KD efficient throughout, what is the protein 
level changes in the KDs, etc. are then important considerations which the above mentioned 
representation of the data could capture. This leads to the important concern that can DNMT3 be 
attributed to all the methylation changes as suggested! It being the de novo catalytic enzyme, 
should/could be a key component. However one cannot exclude other factors. Since DNMT1 is also 
known to possess de novo activity, one cannot completely rule out DNMT1. 
Further in Fig. 3b, late transition cells have similar hypermethylation in the DNMT3A and DNMT3B 
KD in contrast to the conclusion that “DNMT3B knockdown cells fail to hypermethylate to the same 
extent as control cells and DNMT3A knockdown cells show only a partial reduction in methylation”. 
And the lack of hypermethylation in the DNMT3A and DNMT3B KD is confined to a set of probes 
that have 0.2 to 0.4 beta-values, while the sites that have gained high methylation tend to remain 
hyper hypermethylated even in the KDs. 
The bottom line is the mechanistic links are not so clear, and it is still misleading to state that “We 
find that de novo methylation is dependent on DNMT3A” (abstract) given the uncertainty. The rest 
of the paper (the chromatin state links, overlap with cancer methylation, “a putative role of the de 
novo methyltransferases in stabilization of the naïve pluripotent state” etc.) stands firm without 
the mechanistic links. Inclusion of mechanism then should be discussed with the proper caveats. 
This reviewer agrees that it is mot trivial to get at the mechanisms by KD/KO experiments because 
it affects viability/differentiation potential. etc. which are important components of the 
reprogramming model. Discussing the caveats will provide a proper perspective about the 
complexity. 
 
 
4) KO of both 3A1 and 3A2 would have been a critical experiment at least to resolve the 
mechanistic basis of the role of the isoforms of 3A (as suggested by R2). KO of 3A1 but not 3A2 is 
attributed to lack of commercial shRNA targeting 3A2. Does this lack of available shRNA mean 
inability to design good shRNA? Whatever the case, this can be mentioned in methods. 

 
 
Minor: 
Fig. 6c middle panel y-axis scale: does it make sense to have the scale to 150% methylation? 
Fig. 7a: Better to show that the loci shown are bivalent in the figure color legend. 
 
 
 
Reviewer #2: 
Remarks to the Author: 
In this revised version the authors have solved several of the initial concerns, such as the 
presented correlation analysis and new analysis Figure 1 and 2. The addition of the experiments in 
SUSD2+ cells also improved their results. The authors have now used the same definition for 
hypermethylation (10%) across the manuscript, which makes more sense. 
They have also removed the links to Nanog as they have not a direct mechanism connecting it, as 
the authors indicated in the rebuttal, it was by “exclusion”….which is very weak. 
 
However, I believe that there still several aspects that remain not answered correctly and 
therefore making some of the conclusions weak. For example, the leakiness of the system has not 
been tested and the given explanation does not address the potential problem. 
 
More importantly, I still believe that the main message “the mechanistic link between naïve and 
cancer” is not well supported. There are few examples displayed, the differences in methylation in 
these regions are small. Also, the proportion of these overlapping regions is not clear. 
Supplementary Figure 9 shows some of these proportions, but they are related to “random” which 
is not optimal. If this link is going to be made, the authors should show clearly (using the same 
definition for hypermethylation in both systems) the number of these regions in the Naïve 
resetting and in all these different cancers. Then a p-value (expected vs unexpected) can be 
calculated for the common regions and the non-common regions. 
In my opinion, although the new analysis on H3K27me3 is interesting, is not enough to strengthen 
the link that the authors claim. 
 
Finally, as mentioned before the authors should considered to change the word “reprogramming”. 
The given explanation is not satisfactory; indeed it increased my concern. As the authors pointed 
out, there are now reports of “reprogramming” somatic cells into naïve pluripotency and for the 
entire field the use of the term reprogramming indicates that. Meanwhile, resetting or toglelling 
indicate Primed to naïve. This will mislead the readers. The authors stated that these regions are 
common to all naïve states regardless of how they are created. However, they have not done their 
analysis on all these different naïve cells. Furthermore, if this were the case, they should not use 
the term reprogramming at all, and just use “naïve condition” since as they claim, they are not 
studying the specific regions that change between primed and naïve but hypermethylated regions 
common to any naïve state (which they will need to prove). 
Is the authors insist on using the term reprogramming, they should add to the tittle 
"Reprogramming from Primed to Naive pluripotency..." so there is not confusion.