Completed on 20 Apr 2016 by Robin Andersson .
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The recent BioRxiv preprint by Robert Young et al. entitled “Bidirectional transcription marks accessible chromatin and is not specific to enhancers”  is a rather controversial manuscript with strong claims. It caught my attention because it touches upon the research we are conducting in my lab, and refers frequently in its comparisons to one of the FANTOM consortium papers inferring enhancer activity from enhancer transcription , on which I am a first author.
In their preprint, Young et al. draw two major conclusions:
In this post I mainly focus on the first claim. The second claim very much agrees with our own previous analyses on evolutionary conservation of enhancer transcription units (TUs) and also with the fact that most eRNAs are rapidly degraded in the nucleus  . (For an overview of how the fate of these RNAs are determined and how the cell deals with pervasive transcription see these recent reviews  .) Just as a minor comment I want to point out that the focus on multi-exonic eRNAs bias the analysis to a very small fraction of eRNAs (see our previous work on this  ) and therefore does not support general conclusions about eRNAs as a group. However, assuming functional eRNAs are more stable, the fraction of eRNAs with potential function likely belong to this minority group as splicing is strongly related to RNA stability .
The current preprint joins the debate on how to best predict active enhancers in mammalian genomes. During the last ten years the standard practice has mainly been to predict activity based on histone modifications and/or TF or co-activator binding (see my previous review  for an overview of some approaches). Several recent studies (e.g.  and ) have, however, suggested that such predictions contain a large fraction of false positives. Despite this, the field is today highly dogmatized on what constitutes a proper enhancer. This is apparent in the manuscript by Young et al. in their trust in chromatin state predictions of types of regulatory regions and that these states represent functionally distinct units.
While core promoter regions are quite straightforward to identify with current accurate sequencing approaches, e.g. CAGE (5’ end sequencing of cap-selected RNAs) and GRO-cap (5’ end sequencing of cap-selected nascent RNAs), enhancer identification is harder. Our approach is based on the identification of loci with divergent transcription initiation producing balanced amount of eRNAs on both strands. This is challenging because eRNAs are often low abundant and rapidly degraded in the nucleus by the 3’-5’ exoribonucleolytic exosome complex. I therefore welcome studies in which our approach is challenged and may point us in directions on how to improve. However, we first have to assess the reliability of methods and claims by Young et al.
Young et al. claim that bidirectional transcription is not specific to enhancers. I strongly agree with this claim and would even propose that the vast majority of human transcription initiation events are coupled with proximal upstream transcription initiation in the other direction (we have previously examined this property of human gene promoters ). So where do our results disagree? It boils down to whether non-gene promoter transcription initiation events are limited to enhancers or whether all open chromatin loci show transcription initiation.
Young et al, utilized CAGE, GRO-cap, GRO-seq, and PRO-seq data to determine transcription initiation levels and directionality at regulatory regions predicted by chromatin state segmentations. Predictions of stability of transcripts were inspired by a recent study by Core et al. . In the present study, the authors state that absence of CAGE signal but presence of GRO-cap, PRO-seq or GRO-seq signal identifies unstable RNAs, while presence of CAGE and any of the other identifies stable RNAs. At comparable sequencing depths and comparable genomic positional distributions, the identification of unstable transcripts by presence of GRO-cap and absence of CAGE reads is rather elegant. In its original form, Core et al. compared TSS-focused reads (GRO-cap) with CAGE, while Young et al. also include TSS-unspecific reads (GRO-seq and PRO-seq). This may easily affect results when intragenic reads from the latter two sequencing methods (but not GRO-cap) overlap putative regulatory regions. For instance, CTCF-promoted RNA polymerase II pausing (e.g. ) in introns will likely generate local accumulation of non-TSS GRO-seq or PRO-seq reads. Secondly, presence of CAGE reads and reads from nascent RNA sequencing approaches (even if TSS specific) does not necessarily mean that the RNA is stable. Note that the CAGE data used by Young et al. is the very same that was used by us to identify enhancers, whose produced RNAs are mostly unstable. I would recommend the authors to restrict their TSS analyses to GRO-cap and CAGE and for stability measures use data in which an RNA decay pathway has been perturbed (like the HeLa-S3 exosome knockdown data  produced by us).
So, when their analysis shows that bidirectional transcription is not specific to chromatin state predicted enhancers and that bidirectional transcription is for instance present also at CTCF-bound loci I don’t really trust the results. Transcription initiation at CTCF-bound regions could simply be due to intragenic PRO-seq or GRO-seq signal, i.e. not at real TSSs as mentioned above. In addition, other studies (e.g. ) suggest that most CTCF sites are in fact untranscribed. Inaccurate classification of regulatory regions from chromatin data or the fact that the regulatory regions considered by Young et al. were defined in a hierarchical manner (i.e. enhancers could be predicted to be promoters as well) could also bias the results. If these predicted regulatory regions are really functionally different could we then really trust the results? Furthermore, Young et al. only required a single CAGE read on each strand at a regulatory locus to call it bidirectionally transcribed. Although CAGE (and GRO-cap) is a quite excellent method, all sequencing techniques are error prone and studies using such data therefore need to carefully assess the signal with respect to sequencing library noise levels. A single CAGE tag is not sufficient to reliably distinguish true signal from noise. What is the expected sequencing noise level in the CAGE (and GRO-cap, GRO-seq, PRO-seq) libraries investigated?
Young et al. further claim that bidirectional transcription is “a by-product of an opening of chromatin at all types of regulatory regions”. This claim is based on two observations. First they observe that the fraction of DHSs with detected transcription is proportional to the strength of the DHS signal. Is this really unexpected? DNase-seq signal is in individual cells binary (indicating open or close) and the signal over a population of cells measures the fraction of cells in agreement, i.e. DNase-seq signal reflects sample cell population heterogeneity in chromatin openness: the fraction of cells in a sample with a locus having open chromatin and being transcribed will determine both the expression and DNase-seq signal of that locus in a measured cell population. They later state that DHS signal shows clear discrimination between chromatin states in their correlation with (most proximal) genic transcription but that enhancer transcription level does not. How can the DHS signal be strongly correlated with local transcription levels and with genic expression levels when its local transcription level is not correlated with genic expression level? Some other apparent issues are 1) the now well-established fact that the most proximal promoter cannot be assumed to be regulated by an enhancer (ideally for such kind of an analysis chromatin interaction data is needed); 2) far from all DHSs are transcribed; 3) RNA polymerase II is not uniformly distributed in the nucleus (tend to co-localize in transcription factories together with multiple active regulatory elements). Furthermore, the order of events (transcription -> opening of DHSs) is not experimentally shown by Young et al., making this an unsupported claim.
Now, let’s get back to the burning point of disagreement: can enhancer RNAs be used to reliably predict enhancer activities? Young et al. state “transcription initiation provides positive predictive value for accessible DNA but no power to discriminate enhancer from non-enhancer”. Since in vitro enhancer reporter assays can only investigate enhancer potential in a quite artificial manner (enhancer close to promoter), regions that positively validate in such assays can be inactive in vivo. Furthermore, a negative validation result doesn’t necessarily mean that the region doesn’t have enhancer potential, due to putative enhancer-promoter preference (but only one minimal promoter is tested for multiple candidate enhancers) and the high background observed at many minimal promoters, which could mask a weak enhancement and result in a false negative. Therefore, statistics (in particular sensitivity) of any approach will be hard to assess when based on in vitro reporter assays. It is also important to point out that candidate sequences need to be selected randomly to not bias the validation results. The practice of testing a list of top candidates will therefore likely favor the validation results, making a comparison of statistics between studies close to meaningless. A technical note on their own assays: if I understand the method section correctly the candidate enhancer is inserted just upstream of the minimal promoter, i.e. there is no polyA site in between that could hinder transcription originating from the candidate enhancer. How will this affect the results?
Despite the issues listed above, one can still test the potential of predicted positives (positive predicted value (PPR): the fraction of predicted positives that validates positively) with enhancer reporter assays. We tested this previously  on randomly selected candidate enhancers and found that, as Young et al. report, around 70% of candidate enhancers predicted from bidirectional transcription validated. In contrast, we found that only around 25% of non-transcribed enhancers predicted from chromatin data did. Hence, their finding that the fraction of chromatin-defined enhancers without detected transcription initiation show significantly lower reporter activity than transcribed candidate enhancers agrees with FANTOM. They further find that bidirectional transcription also occurs at other regulatory regions that do not validate in reporter assays. This would indicate that bidirectional transcription as a marker of enhancers has a high false discovery rate (FDR). Can we trust that the bidirectional transcription initiation events considered in this study are OK (and not noise or intragenic non-TSS reads as discussed above)? I am a bit hesitant to trust the results mainly because of their use of GRO-seq and PRO-seq data to determine TSSs and our previous results  showing that repressive chromatin states tend to be untranscribed (quite a large fraction of repressed regions are in contrast found to be transcribed in the study by Young et al.). I would recommend that the authors provided PPR and FDR statistics for the different approaches. Regardless of chromatin-state prediction, what are the statistics of predictions based on bidirectional transcription alone and according to varying expression cutoffs or signal to noise ratios? In addition, I would recommend that they reproduce their analyses using alternative massive reporter assay data (e.g. ). Will their claims still hold?