Measurement of average decoding rates of the 61 sense codons in vivo

There seemed to be two general concerns, and some specific concerns. The two general concerns were, first, that there were not enough control experiments validating the “Ribosome Residence Time” method; and second, that we did not deal with a relevant, recently‐published paper by Lareau et al.

With regard to the manuscript’s lack of control experiments validating the approach, we agree. When we first conceived the approach, we tested and validated it several ways, but then, when it became clear that the method worked, we lost interest in validation, moved on to getting results, and neglected to put the validation experiments into the manuscript. This was a mistake. Readers need to know what the evidence is that the approach really works. Reviewer 3 asked for some specific experiments, which we had previously done, but didn’t show. We now have a new Figure (new Figure 2) with four panels, and a new Table (Table 1) showing some of our validation experiments, and these include most of what reviewer 3 requested. We think these experiments are very convincing. Inclusion of this validation material makes the manuscript somewhat longer. If this is a critical concern, this material could be moved to the supplement.

The second major concern was that we did not deal with a highly‐relevant paper, Lareau et al., May, 2014. We had finished writing our manuscript in April, before the Lareau paper came out. For various reasons, we did not submit the manuscript to eLife until June, and in the meantime we did not follow the relevant literature as closely as we should have. We were not aware of the Lareau paper until the reviewers pointed it out. Of course, it is a highly relevant paper that needs to be addressed. We have addressed it in this revised manuscript in a fair amount of detail. The biggest impact is that the Lareau paper provides us with short footprints from anisomycin arrest, and we have applied our method to these short footprints. The new results obtained are in our opinion really interesting, and they are described in a new section of text, a new Figure, and a new Table. We agree with Lareau et al that these short footprints are reporting on a different translational event than the long footprints, so the analysis of the short footprints does not in any way conflict with any of our previous conclusions, but does give us significant new conclusions. We also think it is striking that, although we think the Lareau et al. analysis was very good, nevertheless our analysis got quite a bit more out of the short footprint data, showing the value of our new method. Finally, Lareau et al. got some long footprints without use of cycloheximide, and when we analyzed these by our methods, we got a reasonable correlation (0.47) with our results, which argue that cycloheximide is not introducing severe artefacts.

1) The authors suggest that AT rich codons are decoded more rapidly than GC rich codons but this is not clearly shown in the manuscript. At first this seemed counterintuitive but the authors suggest an interesting possibility that for GC rich codons incorrect tRNAs might dwell in the A site longer than they would at weaker codons and the aggregate of those non-productive interactions might increase the step time at these codons. The authors do not cite any biochemical studies that would support this conclusion and in fact they do not cite previous biochemical studies in the manuscript in many places where that would be appropriate.

We have cited more biochemical studies, including four relevant to the AT vs GC codon issue. But we are hesitant to go too far down this path. There have been many biochemical studies, and they have come to all sorts of conclusions, often conflicting, and in some cases we are just unable to evaluate these studies. We cannot cite them all, and we are uncomfortable with picking through them and citing the ones that are, in hindsight, compatible with our conclusions. So, we are citing a few, including ones we think are highly relevant, and reviews.

We have also added further information on the relative RRTs of GC vs AT rich codons, and done a statistical test, which indeed shows a significant difference between the AT‐rich codons and the GC‐rich codons (p < 0.003).

2) The manuscript at many places simply states conclusions without providing any reference (where that would be appropriate) or argument for the conclusion. Substantiation of the conclusions must be included.

No examples were given, so we are not sure exactly what conclusions are being referred to. We have gone through the manuscript looking for such cases, and have tried hard to add citations, or otherwise provide a reason. If the revised manuscript still has this defect, we would be happy to provide further citations if the reviewers will point out the relevant statements.

3) The major critique of the more critical reviewer is as follows: “Two of the datasets used in the manuscript were previously published by the same group and two have not been published before, however the authors state that the other two were also obtained ”for other reasons in the Futcher lab“. Therefore while the manuscript provides some newly generated experimental data, the primary focus is on computational analysis and in particular on RRT. How valuable and useful is RRT? This, unfortunately, is not very clear. The very fact that it correlates with codon usage merits further investigation as it may indeed provide potentially useful characteristic for decoding rates distributions of the codons with the same sequence. Unfortunately RRT is poorly characterized in the manuscript. Its relationship to the decoding is not explored beyond correlations with codon usage. Also the manuscript misleadingly treats RRT as a measure (rather than potentially related statistics) of codon decoding rates.”

Yes. As we said above, we had originally done validation experiments, but (wrongly) neglected to put them in the manuscript. The new Figure 2 now shows the results of four of our validation experiments. There is a positive and a negative control with simulated data; of these, the negative control with simulated data is the experiment reviewer 3 requested. There is also a positive and a negative control with real data (positive was a serine starvation experiment; negative was the RRT analysis of RNA seq data (i.e., 30 bp RNA fragments, but no footprinting). These two were also essentially experiments the reviewer asked for. The reviewer also asked about analysis of the histidine starvation data in the Lareau paper as another positive control, and we analyzed these data and give the result in the text. We will not go through these experiments in detail here, as we hope they are clear in the revised manuscript. Additional points:

4) The title “Measurement of decoding rates of all individual codons in vivo” is highly misleading.

Lys codon AAA at a position i of mRNA x is not the same as Lys codon AAA at a position j of mRNA y. AAAix and AAAjy likely would have different decoding rates. It would be wonderful to be able to measure decoding rates of individual codons, but this is not the case here. RRT is a relative footprint density of individual codons within a window of 10 neighbor codons averaged over all codons that share the same sequence.

We have changed the title.

5) Before averaging, it makes sense to show that the average is a useful characteristic of the distribution. It would be the case if the distributions were normal or at least could be approximated to normal, as this might not be the case.

If the distributions are not normal, the authors may explore other descriptive statistics of the distribution (for example median) for their relationship with codon usage, tRNA gene copy number or tAI. But it is highly important to obtain descriptive statistics of the distributions first. Even if the distributions are normal, the dispersion of these distributions may not be the same.

Reviewer 3 asks about the distributions of the window frequencies, and whether the mean is a good summary statistic or not. This was an interesting question. We have now provided information on this point in Materials and methods. To summarize, the distributions are not normal. But the reason is, perhaps, innocuous: we required windows that have at least 20 reads, and three non‐zero positions. But still, quite often, a frequency at a particular position in a particular window is zero, because there are no reads at that position, and so the distributions often have a mode at zero. We think that as the number of reads goes up and up, and the number of positions with zero reads goes down, the distributions would approach normal. The distribution is not one that makes the mean an inappropriate statistic.

In any case, we explored summary statistics other than the mean. We repeated all the analysis using the median instead of the mean. As now reported in Materials and Methods, the Spearman rank correlation between the results using the median and the results using the mean is 0.97. That is, results are essentially identical. We had a conversation amongst ourselves as to whether the mean was slightly better, or the median was slightly better, but with a correlation of 0.97 it didn’t really matter, and the mean contains slightly more information. So we have stayed with the mean. We feel that when two summary statistics, the mean and the median, give the same answer, the results must be robust.

6) The procedure for RRT may have a hidden relationship with the codon usage, thus explaining the observed correlation. This could be the case because of intrinsic non-randomness of codon sequences, which effect codon distributions within the 10-codon window. Say a codon X may appear more frequently in the windows centered around the codon Y than in the windows centered around the codon Z. To explore whether there is a hidden relationship to codon usage, the authors should assign experimental footprint densities to codons randomly. Then calculate RRTs and explore how obtained RRT values relate to the codon usage.

In addition to that it would make sense to carry out RRT calculations for naked mRNA controls and explore obtained distributions in a similar manner.

We went through the negative control procedure the reviewer suggests, and there is no signal; all the RRT values come out to essentially 1. This is what is shown in Figure 2A. But also, this procedure is implicit in our method for calculating p‐values for the RRT scores (Table 2, Methods and Materials). That is, the small p‐values imply that in the randomization experiment, there is not any strong signal. Also, as suggested, we did the RRT calculations for naked mRNA controls, and again there is no signal (except at the termini due to enzyme base specificity); this is shown in Figure 2C.

7) Does RRT really relate to codon decoding rates? Intuitively it should, but this needs to be shown. We know from a number of experiments, including ribosome profiling that concentration of tRNAs effect the decoding rates. There are publicly available datasets where particular aminoacylated tRNAs were depleted, see for example Lareau et al 2014 eLife [PMID: 24842990] for S. cerevisiae or Li et al 2012 Nature [PMID:22456704] for bacterial organisms. There might be more. The authors should calculate RRT for these datasets and characterize RRTs between these datasets.

The reviewer suggests we look at the dataset for serine‐starved E. coli. We had previously done this but not shown it; it was one of our first tests of the method. The RRT analysis shows big peaks for the serine codons, and this is now shown in Figure 2D and the accompanying Table. We also looked, less successfully, at the Lareau data for histidine starvation. This is now described in the text. It was less successful because the Lareau dataset for histidine starvation was actually rather small, too small for RRT analysis as described here. Nevertheless, with relaxed quality filters, we did see good‐sized peaks for the two His codons in the 3‐AT treated cultures, but, importantly, not in the non‐starved cultures. We are not putting the figure in the paper, because it is not real RRT analysis, because we had to relax the quality filters to get enough windows.

8) If RRT is indeed a good statistics it should work well not only in yeast, but also in other organisms, thus it is important to carry similar analysis on other publicly available datasets. The authors did that for the very first ribosomal profiling dataset Ingolia et al 2009 dataset, which was generated with cycloheximide pretreatment. It also has a relatively poor coverage. For yeast it would be advisable to use Lareau et al 2014 Elife [PMID: 24842990] data.

RRT should also correlate with other ways of measuring elongation speed. For example, the authors could calculate RRT for Ingolia et al 2011 Cell [PMID: 22056041] and explore whether an aggregated RRTs for the codons of individual coding sequences could predict differences in the speed of ribosomes over individual mRNAs estimated with the pulse chase experiment described in this work.

Yes, the method works well in other organisms. You now see some evidence of that here. We have analysed a lot of existing ribosome profiling data for various organisms from databases. Obviously we cannot put it all in this manuscript. Several quite interesting things have come out of this analysis, and we are in the early stages of planning additional manuscripts. However, we did apply the method to the Lareau et al cycloheximide datasets, and do now report the results here in this manuscript. The correlations with our results are on the low side; 0.2 to 0.5, but still, they are all positive correlations, and we strongly believe that they are relatively modest because Lareau, like Ingolia, add cycloheximide first, then grow the cells a bit, then harvest, whereas we flash‐freeze first, then add cycloheximide to the frozen cells.

The fact that it works well with data in databases from other organisms is of course a reason to publish the paper, so that others will have access to these methods and can also do this analysis.

9) The critical reviewer is skeptical regarding the use of ribosomal profiling data for estimating decoding rates for several reasons. The time that ribosome spends at a particular codon is only one of the factors affecting the number of footprints aligning to that codon. The others are sequence coverage (i), initiation rate for the start codon of corresponding ORF (ii) and concentration of corresponding mRNA (iii). These factors can be estimated (e.g. mRNA-seq can estimate relative mRNA levels) or the data could be normalized in the ways that would minimize the contribution of these factors, e.g. a footprint density at a particular location can be normalized over the cumulative density for the entire dataset or for individual mRNAs. Such normalization procedures aren't perfect and may generate certain artifacts and Gardin et al do discuss it rightfully to some extent. However, there are other factors that are more difficult to take into account, such as the effect of antibiotics on capture of the ribosomes at particular locations or even at specific ribosomal conformations leading to differing length of footprints, see Lareau et al 2014 eLife [PMID: 24842990] for more information. The reviewer is also surprised and disappointed that this very important and highly relevant article is not mentioned in the manuscript.

The other factors effecting densities are those related to the biases of cDNA library preparation. Their presence can be easily seen in the data analyzed here with RRT as well, e.g. Figure 2B; codon 10 corresponds to the 5' ends of the footprints and show a variability comparable to that of position 6 (btw plotting 64 curves on the same diagram is not very effective, the authors should explore other statistics for measuring variability within a distribution). Most likely this variability is due to sequence specificity of RNAse cleavage and/or adapter ligation. The other factor that is highly relevant to measuring decoding rates is PCR amplification of cDNA libraries. PCR amplifies fragments non-linearly, and the ratio between a low abounded fragment and a highly abounded fragment would likely increase after PCR. To control for that the initial step of cDNA amplification should be carried out with RT primers containing random indexes. So that only sequences corresponding to unique ribosome protected fragments are counted. The reviewer understands that doing ribosome profiling this way would require a new experiment and he does not expect the authors doing it for this work, but the issue needs to be at least caveated.

The thrust of point 9 seems to be that we should be able to get similar results by other methods, by estimating the sizes of various effects. Well, maybe. But we are not pursuing other methods; we are trying to describe this one. Also, as we say at the beginning of this manuscript, we think the estimates and guesses involved in making the calculations the reviewer suggests are problematic, and quite likely to lead to the wrong answer. That our approach by‐passes all this guessing and estimating is a lot of the point.

The reviewer also mentions the well‐known fact that PCR can create sampling artefacts. But if any method can defeat PCR sampling problems, it is this one, because we simply consider each and every window as an independent experiment, no matter the frequency of reads in that window. Relatively rare PCR sampling artefacts will affect one window at a time (out of thousands) and so have a negligible impact on our approach. The fact that we have correlations up to 0.96 between our experiments demonstrates that random noise such as introduced by PCR sampling artefacts cannot be a big issue.

Yes, we need to cite and write about Lareau et al. We are sorry to have missed this paper, and thank the reviewers for pointing it out. The revised manuscript talks extensively about the Lareau et al. results, which are really interesting.