Author Response:
The following is the authors’ response to the previous reviews
Reviewer #1 (Public Review):
Summary
While DNA sequence divergence, differential expression, and differential methylation analysis have been conducted between humans and the great apes to study changes that "make us human", the role of lncRNAs and their impact on the human genome and biology has not been fully explored. In this study, the authors computationally predict HSlncRNAs as well as their DNA Binding sites using a method they have developed previously and then examine these predicted regions with different types of enrichment analyses. Broadly, the analysis is straightforward and after identifying these regions/HSlncRNAs the authors examined their effects using different external datasets.
I no longer have any concerns about the manuscript as the authors have addressed my comments in the first round of review.
We thank the reviewer for the valuable comments, which have helped us improve the manuscript.
Reviewer #2 (Public Review):
Lin et al attempt to examine the role of lncRNAs in human evolution in this manuscript. They apply a suite of population genetics and functional genomics analyses that leverage existing data sets and public tools, some of which were previously built by the authors, who clearly have experience with lncRNA binding prediction. However, I worry that there is a lack of suitable methods and/or relevant controls at many points and that the interpretation is too quick to infer selection. While I don't doubt that lncRNAs contribute to the evolution of modern humans, and certainly agree that this is a question worth asking, I think this paper would benefit from a more rigorous approach to tackling it.
I thank the authors for their revisions to the manuscript; however, I find that the bulk of my comments have not been addressed to my satisfaction. As such, I am afraid I cannot say much more than what I said last time, emphasising some of my concerns with regards to the robustness of some of the analyses presented. I appreciate the new data generated to address some questions, but think it could be better incorporated into the text - not in the discussion, but in the results.
We thank the reviewer for the careful reading and valuable comments. In this round of revision, we address the two main concerns: (1) there is a lack of suitable methods and/or relevant controls at many points, and (2) the interpretation is too quick to infer selection. Based on these comments, we have carefully revised all sections of the manuscript, including the Introduction, Results, Discussion, and Materials and Methods.
In addition, we have performed two new analyses. Based on the two analyses, we have added one figure and two sections to Results, two sections to Materials and Methods, one figure to Supplementary Notes, and two tables to Supplementary Tables. These results were obtained using new methods and provided more support to the main conclusion.
To be more responsible, we re-look into the comments made in the first round and respond to them further. The following are point-to-point responses to comments.
Since many of the details in the Responses-To-Comments are available in published papers and eLife publishes Responses-To-Comments, we do not greatly revise supplementary notes to avoid ostensibly repeating published materials.
“lack of suitable methods and/or relevant controls”.
We carefully chose the methods, thresholds, and controls in the study; now, we provide clearer descriptions and explanations.
(1) We have expanded the last paragraph in Introduction to briefly introduce the methods, thresholds, and controls.
(2) In many places in Results and Materials and Methods, revisions are made to describe and justify methods, thresholds, and controls.
(3) Some methods, thresholds, and controls have good consensus, such as FDR and genome-wide background, but others may not, such as the number of genes that greatly differ between humans and chimpanzees. Now, we describe our reasons for the latter situation. For example, we explain that “About 5% of genes have significant sequence differences in humans and chimpanzees, but more show expression differences due to regulatory sequences. We sorted target genes by their DBS affinity and, to be prudential, chose the top 2000 genes (DBS length>252 bp and binding affinity>151) and bottom 2000 genes (DBS length<60 bp but binding affinity>36) to conduct over-representation analysis”.
(4) We also carefully choose proper words to make descriptions more accurate.
Responses to the suggestion “new data generated could be better incorporated into the text”.
(1) We think that this sentence “The occurrence of HS lncRNAs and their DBSs may have three situations – (a) HS lncRNAs preceded their DBSs, (b) HS lncRNAs and their DBSs co-occurred, (c) HS lncRNAs succeeded their DBSs. Our results support the third situation and the rewiring hypothesis”, previously in Discussion, should be better in section 2.3. We have revised it and moved it into the second paragraph of section 2.3.
(2) Our two new analyses generated new data, and we describe them in Results.
(3) It is possible to move more materials from Supplementary Notes to the main text, but it is probably unnecessary because the main text currently has eight sub-sections, two tables, and four figures.
Responses to the comment “the interpretation is too quick to infer selection”.
(1) When using XP-CLR, iSAFE, Tajima's D, Fay-Wu's H, the fixation index (Fst), and linkage disequilibrium (LD) to detect selection signals, we used the widely adopted parameters and thresholds but did not mention this clearly in the original manuscript. Now, in the first sentence of the second paragraph of section 2.4, we add the phrase “with widely-used parameters and thresholds” (more details are available in section 4.7 and Supplementary Notes).
(2) It is not the first time we used these tests. Actually, we used these tests in two other studies (Tang et al. Uncovering the extensive trade-off between adaptive evolution and disease susceptibility. Cell Rep. 2022; Tang et al. PopTradeOff: A database for exploring population-specificity of adaptive evolution, disease susceptibility, and drug responsiveness. Comput Struct Biotechnol J. 2023). In this manuscript, section 2.5 and section 4.12 describe how we use these tests to detect signals and infer selection. We also cite the above two published papers from which the reader can obtain more details.
(3) Also, in section 2.4, we stress that “Signals in considerable DBSs were detected by multiple tests, indicating the reliability of the analysis”.
To further respond to the comments of “lack of suitable methods” and “this paper would benefit from a more rigorous approach to tackling it”, we have performed two new analyses. The results of the new analyses agree well with previous results and provide new support for the main conclusion. The result of section 2.5 is novel and interesting.
We write in Discussion “Two questions are how mouse-specific lncRNAs specifically rewire gene expression in mice and how human- and mouse-specific rewiring influences the cross-species transcriptional differences”. To investigate whether the rewiring of gene expression by HS lncRNA in humans is accidental in evolution, we have made further genomic and transcriptomic analyses (Lin et al. Intrinsically linked lineage-specificity of transposable elements and lncRNAs reshapes transcriptional regulation species- and tissue-specifically. doi: https://doi.org/10.1101/2024.03.04.583292). To verify the obtained conclusions, we analyzed the spermatogenesis data from multiple species and obtained supporting evidence (not published).
I note some specific points that I think would benefit from more rigorous approaches, and suggest possible ways forward for these.
Much of this work is focused on comparing DNA binding domains in human-unique long-noncoding RNAs and DNA binding sites across the promoters of genes in the human genome, and I think the authors can afford to be a bit more methodical/selective in their processing and filtering steps here. The article begins by searching for orthologues of human lncRNAs to arrive at a set of 66 human-specific lncRNAs, which are then characterised further through the rest of the manuscript. Line 99 describes a binding affinity metric used to separate strong DBS from weak DBS; the methods (line 432) describe this as being the product of the DBS or lncRNA length times the average Identity of the underlying TTSs. This multiplication, in fact, undoes the standardising value of averaging and introduces a clear relationship between the length of a region being tested and its overall score, which in turn is likely to bias all downstream inference, since a long lncRNA with poor average affinity can end up with a higher score than a short one with higher average affinity, and it's not quite clear to me what the biological interpretation of that should be. Why was this metric defined in this way?
(1) Using RNA:DNA base-pairing rules, other DBS prediction programs return just DBSs with lengths. Using RNA:DNA base-pairing rules and a variant of Smith-Waterman local alignment, LongTarget returns DBSs with lengths and identity values together with DBDs (local alignment makes DBDs and DBSs predicted simultaneously). Thus, instead of measuring lncRNA/DNA binding based on DBS length, we measure lncRNA/DNA binding based on both DBS length and DBD/DBS identity (simply called identity, which is the percentage of paired nucleotides in the RNA and DNA sequences). This allows us to define “binding affinity”. One may think that binding affinity is a more complex function of length and identity. But, according to in vitro studies (see the review Abu Almakarem et al. 2012 and citations therein, and see He et al. 2015 and citations therein), the strength of a triplex is determined by all paired nucleotides (i.e., triplet). Thus, binding affinity=length * identity is biologically reasonable.
(2) Further, different from predicting DBS upon individual base-pairing rules such as AT-G and CG-C, LongTarget integrates base-pairing rules into rulesets, each covering A, T, C, and G (see the two figures below, which are from He et al 2015). This makes every nucleotide in the RNA and DNA sequences comparable and allows the computation of identity.
(3) On whether LongTarget may predict unreasonably long DBSs. Three technical features of LongTarget make this highly unlikely (and more unlikely than other programs). The three features are (a) local alignment, (b) gap penalty, and (c) TT penalty (He et al. 2015).
(4) Some researchers may think that a higher identity threshold (e.g., 0.8 or even higher) makes the predicted DBSs more reliable. This is not true. To explore plausible identity values, we analyzed the distribution of Kcnq1ot1’s DBSs in the large Kcnq1 imprinting region (which contains many known imprinted genes). We found that a high threshold for identity (e.g., 0.8) will make DBSs in many known imprinted genes fail to be predicted. Upon our analysis of many lncRNAs and upon early in vitro experiments, plausible identity values range from 0.4 to 0.8.
(5) Is it necessary or advisable to define an identity threshold? Since identity values from 0.4 to 0.8 are plausible and identity is a property of a DBS but does not reflect the strength of the whole triplex, it is more reasonable to define a threshold for binding affinity to control predicted DBSs. As explained above, binding affinity = length*identity is a reasonable measure of the strength of a triplex. The default threshold is 60, and given an identity of 0.6 in many triplexes, a DBS with affinity=60 is about 100 bp. Compared with TF binding sites (TFBS), 100 bp is quite long. As we explain in the main text, “taking a DBS of 147 bp as an example, it is extremely unlikely to be generated by chance (p < 8.2e-19 to 1.5e-48)”.
(6) How to validate predicted DBSs? Validation faces these issues. (a) DBDs are predicted on the genome level, but target transcripts are expressed in different tissues and cells. So, no single transcriptomic dataset can validate all predicted DBSs of a lncRNA. No matter using what techniques and what cells, only a small portion of predicted DBSs can be experimentally captured (validated). (b) The resolution of current experimental techniques is limited; thus, experimentally identified DBSs (i.e., “peaks”) are much longer than computationally predicted DBSs. (c) Experimental results contain false positives and false negatives. So, validation (or performance evaluation) should also consider the ROC curves (Wen et al. 2022).
(7) As explained above, a long DBS may have a lower binding affinity than a short DBS. A biological interpretation is that the long DBS may accumulate mutations that decrease its binding ability gradually.
There is also a strong assumption that identified sites will always be bound (line 100), which I disagree is well-supported by additional evidence (lines 109-125). The authors show that predicted NEAT1 and MALAT1 DBS overlap experimentally validated sites for NEAT1, MALAT1, and MEG3, but this is not done systematically, or genome-wide, so it's hard to know if the examples shown are representative, or a best-case scenario.
(1) We did not make this assumption. Apparently, binding depends on multiple factors, including co-expression of genes and specific cellular context.
(2) On the second issue, “this is not done systematically, or genome-wide”. We did genome-wide but did not show all results (supplementary fig 2 shows three genomic regions, which are impressively good). In Wen et al. 2022, we describe the overall results.
It's also not quite clear how overlapping promoters or TSS are treated - are these collapsed into a single instance when calculating genome-wide significance? If, eg, a gene has five isoforms, and these differ in the 3' UTR but their promoter region contains a DBS, is this counted five times, or one? Since the interaction between the lncRNA and the DBS happens at the DNA level, it seems like not correcting for this uneven distribution of transcripts is likely to skew results, especially when testing against genome-wide distributions, eg in the results presented in sections 5 and 6. I do not think that comparing genes and transcripts putatively bound by the 40 HS lncRNAs to a random draw of 10,000 lncRNA/gene pairs drawn from the remaining ~13500 lncRNAs that are not HS is a fair comparison. Rather, it would be better to do many draws of 40 non-HS lncRNAs and determine an empirical null distribution that way, if possible actively controlling for the overall number of transcripts (also see the following point).
(1) We predicted DBSs in the promoter region of 179128 Ensembl-annotated transcripts and did not merge DBSs (there is no need to merge them). If multiple transcripts share the same TSS, they may share the same DBS, which is natural.
(2) If the DBSs of multiple transcripts of a gene overlap, the overlap does not raise a problem for lncRNA/DNA binding analysis in specific tissues because usually only one transcript is expressed in a tissue. Therefore, there is no such situation “If, e.g., a gene has five isoforms, and these differ in the 3' UTR but their promoter region contains a DBS, is this counted five times, or one?”
(3) It is unclear to us what “it seems like not correcting for this uneven distribution of transcripts is likely to skew results” means. Regarding testing against genome-wide distributions, statistically, it is beneficial to make many rounds of random draws genome-wide, but this will take a huge amount of time. Since more variables demand more rounds of drawing, to our knowledge, this is not widely practiced in large-scale transcriptomic data analyses.
(4) If the difference (result) is small thus calls for rigorous statistical testing, making many rounds of random draws genome-wide is necessary. In our results, “45% of these pairs show a significant expression correlation in specific tissues (Spearman's |rho| >0.3 and FDR <0.05). In contrast, when randomly sampling 10000 pairs of lncRNAs and protein-coding transcripts genome-wide, the percent of pairs showing this level of expression correlation (Spearman's |rho| >0.3 and FDR <0.05) is only 2.3%”.
Thresholds for statistical testing are not consistent, or always well justified. For instance, in line 142 GO testing is performed on the top 2000 genes (according to different rankings), but there's no description of the background regions used as controls anywhere, or of why 2000 genes were chosen as a good number to test? Why not 1000, or 500? Are the results overall robust to these (and other) thresholds? Then line 190 the threshold for downstream testing is now the top 20% of genes, etc. I am not opposed to different thresholds in principle, but they should be justified.
(1) We used the g:Profiler program to perform over-representation analysis to identify enriched GO terms. This analysis is used to determine what pre-defined gene sets (GO terms) are more present (over-represented) in a list of “interesting” genes than what would be expected by chance. Specifically, this analysis is often used to examine whether the majority of genes in a pre-defined gene set fall in the extremes of a list: the top and bottom of the list, for example, may correspond to the largest differences in expression between the two cell types. g:Profiler always takes the whole genome as the reference; that is why we did not mention the whole genome reference. We now add in section 2.2 “(with the whole genome as the reference)”.
(2) Why choosing 2000 but not 2500 genes is somewhat subjective. We now explain that “About 5% of genes have significant sequence differences in humans and chimpanzees, but more show expression differences due to regulatory sequences. We sorted target genes by their DBS affinity and, to be prudential, chose the top 2000 genes (DBS length>252 bp and binding affinity>151) and bottom 2000 genes (DBS length<60 bp but binding affinity>36) to conduct over-representation analysis”.
Likewise, comparing Tajima's D values near promoters to genome-wide values is unfair, because promoters are known to be under strong evolutionary constraints relative to background regions; as such it is not surprising that the results of this comparison are significant. A fairer comparison would attempt to better match controls (eg to promoters without HS lncRNA DBS, which I realise may be nearly impossible), or generate empirical p-values via permutation or simulation.
We used these tests to detect selection signals in DBSs but not in the whole promoter regions. Using promoters without HS lncRNA DBS as the control also has risks because promoter regions contain other kinds of regulatory sequences.
There are huge differences in the comparisons between the Vindija and Altai Neanderthal genomes that to me suggest some sort of technical bias or the such is at play here. e.g. line 190 reports 1256 genes to have a high distance between the Altai Neanderthal and modern humans, but only 134 Vindija genes reach the same threshold of 0.034. The temporal separation between the two specimens does not seem sufficient to explain this difference, nor the difference between the Altai Denisovan and Neanderthal results (2514 genes for Denisovan), which makes me wonder if it is a technical artefact relating to the quality of the genome builds? It would be worth checking.
We feel it is hard to know whether or not the temporal separation between these specimens is sufficient to explain the differences because many details of archaic humans and their genomes remain unknown and because mechanisms determining genotype-phenotype relationships remain poorly known. After 0.034 was determined, these numbers of genes were determined accordingly. We chose parameters and thresholds that best suit the most important requirements, but these parameters and thresholds may not best suit other requirements; this is a problem for all large-scale studies.
Inferring evolution: There are some points of the manuscript where the authors are quick to infer positive selection. I would caution that GTEx contains a lot of different brain tissues, thus finding a brain eQTL is a lot easier than finding a liver eQTL, just because there are more opportunities for it. Likewise, claims in the text and in Tables 1 and 2 about the evolutionary pressures underlying specific genes should be more carefully stated. The same is true when the authors observe high Fst between groups (line 515), which is only one possible cause of high Fst - population differentiation and drift are just as capable of giving rise to it, especially at small sample sizes.
(1) We add in Discussion that “Finally, not all detected signals reliably indicate positive selection”.
(2) Our results are that more signals are detected in CEU and CHB than in YRI; this agrees all population genetics studies and implies that our results are not wrongly biased because more samples and larger samples were obtained from CEU and CHB.
