No Ramp Needed: Spandrels, Statistics, and a Slippery Slope

Reviewer #1 (Public Review):

The manuscript by Sejour et al. is testing "translational ramp" model described previously by Tuller et al. in S. cerevisiae. Authors are using bioinformatics and reporter based experimental approaches to test whether "rare codons" in the first 40 codons of the gene coding sequences increase translation efficiency and regulate abundance of translation products in yeast cells. Authors conclude that "translation ramp" model does not have support using a new set of reporters and bioinformatics analyses. The strength of bioinformatic evidence and experimental analyses (even very limited) of the rare codons insertion in the reporter make a compelling case for the authors claims. However the major weakness of the manuscript is that authors do not take into account other models that previously disputed "rare or slow codon" model of Tuller et al. and overstate their own results that are rather limited. This maintains to be the weak part of the manuscript even in the revised form.

The studies that authors do not mention argue with "translation ramp" model and show more thorough analyses of translation initiation to elongation transition as well as early elongation "slow down" in ribosome profiling data. Moreover several studies have used bioinformatical analyses to point out the evolution of N-terminal sequences in multiple model organisms including yeast, focusing on either upstream ORFs (uORFs) or already annotated ORFs. The authors did not mention multiple of these studies in their revised manuscript and did not comment on their own results in the context of these previous studies. As such the authors approach to data presentation, writing and data discussion makes the manuscript rather biased, focused on criticizing Tuller et al. study and short on discussing multiple other possible reasons for slow translation elongation at the beginning of the protein synthesis. This all together makes the manuscript at the end very limited.

Reviewer #2 (Public Review):

Tuller et al. first made the curious observation, that the first ∼30-50 codons in most organisms are encoded by scarce tRNAs and appear to be translated slower than the rest of the coding sequences (CDS). They speculated that this has evolved to pace ribosomes on CDS and prevent ribosome collisions during elongation - the "Ramp" hypothesis. Various aspects of this hypothesis, both factual and in terms of interpreting the results, have been challenged ever since. Sejour et al. present compelling results confirming the slower translation of the first ~40 codons in S. cerevisiae but providing an alternative explanation for this phenomenon. Specifically, they show that the higher amino acid sequence divergence of N-terminal ends of proteins and accompanying lower purifying selection (perhaps the result of de novo evolution) is sufficient to explain the prevalence of rare slow codons in these regions. These results are an important contribution in understanding how aspects of the evolution of protein coding regions can affect translation efficiency on these sequences and directly challenge the "Ramp" hypothesis proposed by Tuller et al.

I believe the data is presented clearly and the results generally justify the conclusions.

Author Response

The following is the authors’ response to the current reviews.

Reviewer #1 (Public Review):

The manuscript by Sejour et al. is testing "translational ramp" model described previously by Tuller et al. in S. cerevisiae. Authors are using bioinformatics and reporter based experimental approaches to test whether "rare codons" in the first 40 codons of the gene coding sequences increase translation efficiency and regulate abundance of translation products in yeast cells. Authors conclude that "translation ramp" model does not have support using a new set of reporters and bioinformatics analyses. The strength of bioinformatic evidence and experimental analyses (even very limited) of the rare codons insertion in the reporter make a compelling case for the authors claims. However the major weakness of the manuscript is that authors do not take into account other models that previously disputed "rare or slow codon" model of Tuller et al. and overstate their own results that are rather limited. This maintains to be the weak part of the manuscript even in the revised form.

We are glad the reviewer thinks our evidence makes “a compelling case for the authors claims”. This was our main aim, and we are satisfied with this.

The reviewer believes the major weakness of the manuscript is that we do not take into account other models and do not (see below) cite numerous other relevant papers. The reviewer made essentially the same criticism at the first review, at which time we looked quite hard for papers generally meeting the reviewer’s description. We found a few, which we incorporated here. Still, we did not find the body of evidence whose existence the reviewer implies. We are citing every study we know to be relevant, though of course we will have inadvertently missed some, given the huge body of literature. After the first round of review, we wrote “the reviewer did not give specific references, and, though we looked, we weren’t always sure which papers the reviewer had in mind.” We hoped the reviewer would provide citations. But only two citations are provided here, both to A. Kochetov, and these don’t seem central to the reviewer’s points.

The studies that authors do not mention argue with "translation ramp" model and show more thorough analyses of translation initiation to elongation transition as well as early elongation "slow down" in ribosome profiling data. Moreover several studies have used bioinformatical analyses to point out the evolution of N-terminal sequences in multiple model organisms including yeast, focusing on either upstream ORFs (uORFs) or already annotated ORFs. The authors did not mention multiple of these studies in their revised manuscript and did not comment on their own results in the context of these previous studies.

Mostly, we do not know to what papers the reviewer is referring. This may be our failing, but it would have helped if the reviewer had cited one of them. There are papers discussing the evolution of N-terminal sequences, but as far as we know, these do not discuss translation speed or codon usage. Of course, we may have missed some papers.

As such the authors approach to data presentation, writing and data discussion makes the manuscript rather biased, focused on criticizing Tuller et al. study and short on discussing multiple other possible reasons for slow translation elongation at the beginning of the protein synthesis. This all together makes the manuscript at the end very limited.

We think the reviewer may be considering our paper as being generally about translation speeds, whereas in our minds, it is not. This difference in views as to what the paper is “about” is perhaps causing friction. To us, it is indeed a limited paper. We are narrowly focused on the finding of Tuller that there is an enrichment of rare, slow codons at the 5’ end of genes, and we have sought an explanation of this particular fact. This is not a paper about rates of translation generally—it is a limited paper about the reason for the 5’ enrichment of rare, slow codons.

To expand on this, the encoded slow 5’ translation due to rare, slow codons (of Tuller et al.) is a small effect (1% to 3%). The possible unencoded slow 5’ translation of unknown mechanism discussed by some other papers (e.g., Weinberg et al. 2016, Shah et al. 2013) is a much larger effect (50% or more). Just from the different magnitudes, it seems likely these are different phenomena. And yet, despite the small size of the encoded effect, it is for some reason this paper by Tuller et al. that has captured the attention of the literature: as we point out below, Tuller et al. has been cited over 900 times. Partly because of the wide and continuing influence of this paper, it is worth specifically and narrowly addressing its findings.

Reviewer #2 (Public Review):

Tuller et al. first made the curious observation, that the first ∼30-50 codons in most organisms are encoded by scarce tRNAs and appear to be translated slower than the rest of the coding sequences (CDS). They speculated that this has evolved to pace ribosomes on CDS and prevent ribosome collisions during elongation - the "Ramp" hypothesis. Various aspects of this hypothesis, both factual and in terms of interpreting the results, have been challenged ever since. Sejour et al. present compelling results confirming the slower translation of the first ~40 codons in S. cerevisiae but providing an alternative explanation for this phenomenon. Specifically, they show that the higher amino acid sequence divergence of N-terminal ends of proteins and accompanying lower purifying selection (perhaps the result of de novo evolution) is sufficient to explain the prevalence of rare slow codons in these regions. These results are an important contribution in understanding how aspects of the evolution of protein coding regions can affect translation efficiency on these sequences and directly challenge the "Ramp" hypothesis proposed by Tuller et al.

I believe the data is presented clearly and the results generally justify the conclusions.

We thank the reviewer for his/her attention to the manuscript, and for his/her comments.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

As mentioned in the public review major weakness of the manuscript is the lack of analyses for confounding effects, overstatements of the results (using single amino acid sequence reporter) and the lack of discussion of previous work that argues against Tuller et al model. In my previous review I mentioned multiple other studies that addressed "slow codons" model in more detail.

No, the reviewer did not cite any specific studies.

While some of these studies are mentioned in the revised manuscript, authors are still rather biased and selective in their discussions. I should also point out that previous studies, that authors fail again to mention, were focused on either translation initiation, initiation to elongation transition or early elongation effects in relation to mRNA sequence, structure, codons as well as amino acid sequence. Also additional studies with bioinformatic analyses of N-terminal conservation and existence of start sites at the beginning of the protein sequences in multiple model organisms were also omitted.

Again, we do not know to what papers the reviewer is referring. But this sounds like a lot. Our paper is aimed at a specific, narrow topic: Why is there an excess of rare, slow codons in the 5’ region of genes? We are not trying to make general statements about all things affecting and affected by translation speed, we are just trying to explain the excess of rare, slow codons.

In general manuscript seems to be too much focused-on discussion of Tuller's paper . . .

Yes, we are focused on the Tuller findings, the excess of rare slow codons in 5’ regions.

. . . and arguing with the model that was already shown by multiple other studies to be limited and not correct.

We find it unsatisfactory that the reviewer states in a public review that there are multiple other studies showing that the Tuller model is not correct, and yet does not cite any of them. Furthermore, for the reviewer to say that Tuller et al. is “not correct” is too sweeping. The core finding of Tuller et al. was the excess of rare, slow codons in the 5’ regions of genes. We confirm this; we believe it is correct; we are not aware of any literature disputing this. Then, Tuller interpreted this as an adaptation to promote translational efficiency. On the interpretation, we disagree with Tuller. But if one is to disagree with this interpretation, one needs an alternative explanation of the fact of the excess rare, slow codons. Providing such an alternative explanation, and doing an experiment to distinguish the explanations, is our contribution. We are not aware of any other paper making our interpretation.

There are of course many papers that discuss various aspects of translation at the 5’ ends of genes, and we do cite quite a few such papers in our manuscript, though certainly not all. But papers of this general kind do not, and cannot, show that Tuller et al. is “not correct”. As far as we know, no paper provides an alternative explanation for the rare slow codons, and no paper does an experiment to modulate translation speed and look at the effect on gene expression. Notably, the slow translation phenomenon associated with the rare codons found by Tuller et al. is a very small effect—a change of about 1% to 3% of translation speed. Some other papers on translation speed are dealing with possible changes in the range of 50% or more. These are presumably some other phenomenon (if indeed they are even real changes in translation speed), and, whether they are true or not, the results and interpretations of Tuller et al. could still be true or not. Of course, if we knew of some previous paper showing the Tuller paper is not correct, we should and would cite it.

To expand on the current view of Tuller in the literature, Tuller et al. has been cited 956 times according to Google Scholar. This makes it an extremely influential paper. After finding Tuller et al. in Entrez Pubmed, one can look under “Cited by” and see the five most recent papers that cite Tuller et al. The five papers given on May 23 2024 were Bharti . . . Ignatova 2024; Uddin 2024; Khandia . . . Choudhary 2024; Love and Nair 2024; and Oelschlaeger 2024. We went through these five most recent papers that cite Tuller et al., and asked, did these authors cite the Tuller results as fully correct, or did they mention any doubts about the results? All five of the papers cited the Tuller results as fully correct, with no mention of any kind of doubt. For instance, Kandia et al. 2024 state “The slow “ramp” present at 5’ end of mRNA forms an optimal and robust means to reduce ribosomal traffic jams, thus minimizing the cost of protein expression40.”, while Oelschlaeger (2024) states “Slow translation ramps have also been described elsewhere and proposed to prevent traffic jams along the mRNA [51,52,53].” Although Uddin (2024) cited Tuller as fully correct, Uddin seemed to think (it is a little unclear) that Tuller found an enrichment of highly-used codons, opposite to the actual finding. The multiple contrary studies mentioned by the reviewer do not seem to have been very influential.

There are papers containing skepticism about the Tuller interpretation, and also papers with results that are difficult to reconcile in a common-sense way with the Tuller interpretation. But skepticism, and a difficulty to reconcile with common sense, are far from a demonstration that a paper is incorrect. Indeed, Tuller et al. may have been published in Cell, and may be so highly cited, exactly because the findings are counter-intuitive, colliding with common sense. Our contribution is to find a common-sense interpretation of the surprising but correct underlying fact of the 5’ enrichment of rare, slow codons.

Having wrote that in the previous review, I have to admit that Sejour et al manuscript in the main text has a minimal amount of novelty with experimental evidence, the conclusions are based on three reporters with and without stalling/collision sequence with the same amino acid sequence and varying codons. Some more novelty is seen in bioinformatic analyses of multiple yeast sequences and sequence conservation at the N-termini of proteins. However, even this part of the manuscript is not discussed fully and with correct comparison to previous studies. Authors, based on my previous comments discuss further experimental shortcomings in their new and "expanded" discussion but the use of a single reporter in this case cannot relate to all differences that may be coming from ORFs seen in complete yeast transcriptome. There are multiple studies that used more reporters with more than one amino-acid and mRNA sequence as well as with similar variation of the rare or common codons. The handwaving argument about the influence of all other mechanisms that can arise from different start sites, RNA structure, peptide interaction with exit channel, peptidyl-tRNA drop-off, eIF3 complex initiation-elongation association, and etc, is just pointing up to a manuscript that is more about bashing up Tuller's model and old paper than trying to make a concise story about their own results and discuss their study in plethora of studies that indicated multiple other models for slow early elongation.

We don’t understand why the reviewer is so grudging.

Discussion of the ribosome's collisions and potential impact of such scenario in the author's manuscript is left completely without citation, even though such work has relevant results to the author's conclusions and Tuller's model.

This is not true. We cite Dao Duc and Song (2018) “The impact of ribosomal interference, codon usage, and exit tunnel interactions on translation elongation rate variation.” PLoS Genet 14, and Tesina, . . . and Green (2020) “Molecular mechanism of translational stalling by inhibitory codon combinations and Poly(A) tracts. EMBO J., which are two excellent papers on this subject. We also cite Gamble et al. (2016), who found the underlying result, but at that time did not attribute it to ribosome collisions.

Previous studies (not cited) for example clearly indicate how the length from stalling sequence to start codon is related to ribosome collisions. Moreover such studies are pointing out differences in initiation vs elongation rates that may impact ribosome collisions and protein expression. Both of these topics would be very valuable in discussions of evolutionary changes in the current yeast ORFs. Not to mention that authors do not really discuss also possibilities for differences in 5'UTRs and uORFs in relation to downstream ORFs sequence and codon composition.

It is not clear to us that such papers are highly relevant to the issue on which we are working.

The argument about whether cycloheximide or not is doing 5' ribosome slowdown (lines 425-443) is just rambling about Weinberg's paper from 2016 without any real conclusion. In this section authors are just throwing down hypothesis that were more clearly explained in Weinberg's manuscript or shown experimentally in studies done after the Weinberg et al. paper was published.

Earlier, the reviewer had the criticism that “The studies that authors do not mention argue with "translation ramp" model and show more thorough analyses of translation initiation to elongation transition as well as early elongation "slow down" in ribosome profiling data.” The main study we know of dealing with these issues like these is that of Weinberg et al. 2016. In our opinion, this is a thoughtful paper on these issues. But now, at this point, the reviewer seems to criticize the fact that we do extensively cite results from Weinberg et al. It is true that there is no ultimate conclusion, but why there is no conclusion is a little bit interesting. Weinberg et al show that even in studies that do not use cycloheximide as the first step in ribosome profiling, there is some left-over high density of ribosomes near 5’ ends. But, all these ribosome profiling experiments do use cycloheximide at a later step in the procedure. Until someone does a ribosome profiling experiment without the use of any cycloheximide at any step, there will be no firm conclusion. This is not our fault—and also not the issue we are writing about. And, the reason this paragraph is in the manuscript at all is that the reviewer (we thought) had asked for something like this in the first review.

At the end, even in the limited novelty of evolutionary arguments about non-existing N-terminal conservation of codons or amino acids they fail to cite and discuss previous work by Kochetov (BioEssays, 2008 and NAR, 2011) which have additional explanation on evolution of N-terminal sequences in yeast, human or Drosophila.

These two papers of Dr. Kochetov’s have some relevance and we now cite them. These are the only papers cited by the reviewer in his/her two reviews.

Probably the reviewer would have preferred a paper on a different subject.

The following is the authors’ response to the original reviews.

Response to Reviewers:

We thank the reviewers for their comments, and their evident close reading of the manuscript. Generally, we agree with the reviewers on the strengths and weaknesses of our manuscript. Our revised manuscript has a more extensive discussion of alternative explanations for initial high ribosome density as seen by ribosome profiling, and which more specifically points out the limitations of our work.

As a preface to specific responses to the reviewers, we will say that we could divide observations of slow initial translation into two categories, which we will call “encoded slow codons”, and “increased ribosome density”. With respect to the first category, Tuller et al. documented initial “encoded slow codons”, that is, there is a statistical excess of rare, slowly-translated codons at the 5’ ends of genes. Although the size of this effect is small, statistical significance is extremely high, and the existence of this enrichment is not in any doubt. At first sight, this appears to be a strong indication of a preference for slow initial translation. In our opinion, our main contribution is to show that there is an alternative explanation for this initial enrichment of rare, slow codons—that they are a spandrel, a consequence of sequence plasticity at the 5’ (and 3’) ends of genes. The reviewers seem to generally agree with this, and we are not aware that any other work has provided an explanation for the 5’ enrichment of rare codons.

The second category of observations pertaining to slow initial translation is “increased ribosome density”. Early ribosome profiling studies used cycloheximide to arrest cell growth, and these studies showed a higher density of ribosomes near the 5’ end of genes than elsewhere. This high initial ribosome density helped motivate the paper of Tuller et al., though their finding of “encoded slow codons” could explain only a very small part of the increased ribosome density. More modern ribosome profiling studies do not use cycloheximide as the first step in arresting translation, and in these studies, the density of ribosomes near the 5’ end of genes is greatly reduced. And yet, there remains, even in the absence of cycloheximide at the first step, a significantly increased density of ribosomes near the 5’ end (e.g., Weinberg et al., 2016). (However, most or all of these studies do use cycloheximide at a later step in the protocol, and the possibility of a cycloheximide artefact is difficult to exclude.) Some of the reviewer’s concerns are that we do not explain the increased 5’ ribosome density seen by ribosome profiling. We agree; but we feel it is not the main point of our manuscript. In revision, we more extensively discuss other work on increased ribosome density, and more explicitly point out the limitations of our manuscript in this regard. We also note, though, that increased ribosome density is not a direct measure of translation speed—it can have other causes.

Specific Responses.

Reviewer 1 was concerned that we did not more fully discuss other work on possible reasons for slow initial translation. We discuss such work more extensively in our revision. However, as far as we know, none of this work proposes a reason for the 5’ enrichment of rare, slow codons, and this is the main point of our paper. Furthermore, it is not completely clear that there is any slow initial translation. The increase in ribosome density seen in flash-freeze ribosome profiling could be an artefact of the use of cycloheximide at the thaw step of the protocols; or it could be a real measure of high ribosome density that occurs for some other reason than slow translation (e.g., ribosomes might have low processivity at the 5’ end).

Reviewer 1 was also concerned about confounding effects in our reporter gene analysis of the effects of different codons on efficiency of translation. We have two comments. First, it is important to remember that although we changed codons in our reporters, we did not change any amino acids. We changed codons only to synonymous codons. Thus at least one of the reviewer’s possible confounding effects—interactions of the nascent peptide chain with the exit channel of the ribosome—does not apply. However, of course, the mRNA nucleotide sequence is altered, and this would cause a change in mRNA structure or abundance, which could matter. We agree this is a limitation to our approach. However, to fully address it, we feel it would be necessary to examine a really large number of quite different sequences, which is beyond the scope of this work. Furthermore, mRNAs with low secondary structure at the 5’ end probably have relatively high rates of initiation, and also relatively high rates of elongation, and it might be quite difficult to disentangle these. But in neither case is there an argument that slow initial translation is efficient. Accurate measurement of mRNA levels would be helpful, but would not disentangle rates of initiation from rates of elongation as causes of changes in expression.

Reviewer 2 was concerned that the conservation scores for the 5’ 40 amino acids, and the 3’ 40 amino acids were similar, but slow translation was only statistically significant for the 5’ 40 amino acids. As we say in the manuscript, we are also puzzled by this. We note that 3’ translation is statistically slow, if one looks over the last 100 amino acids. Our best effort at an explanation is a sort of reverse-Tuller explanation: that in the last 40 amino acids, the new slow codons created by genome plasticity are fairly quickly removed by purifying selection, but that in the first 40 amino acids, for genes that need to be expressed at low levels, purifying selection against slow codons is reduced, because poor translation is actually advantageous for these genes. To expand on this a bit, we feel that the 5000 or so proteins of the proteome have to be expressed in the correct stoichiometric ratios, and that poor translation can be a useful tool to help achieve this. In this explanation, slow translation at the 5’ end is bad for translation (in agreement with our reporter experiments), but can be good for the organism, when it occurs in front of a gene that needs to be expressed poorly. Whereas, in Tuller, slow translation at the 5’ end is good for translation.

Reviewer 2 wondered whether the N-terminal fusion peptide affects GFP fluorescence in our reporter. This specific reporter, with this N-terminus, has been characterized by Dean and Grayhack (2012), and by Gamble et al. (2016), and the idea that a super-folder GFP reporter is not greatly affected by N-terminal fusions is based on the work of Pedelacq (2006). None of these papers show whether this N-terminal fusion might have some effect, but together, they provide good reason to think that any effect would be small. These citations have been added.