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In a previous post I wrote about How not to perform a differential expression analysis. In response to my post, Rob Patro, Geet Duggal, Michael I Love, Rafael Irizarry and Carl Kingsford wrote a detailed response. Below is my point-by-point rebuttal to their response (the figures and results in this blog post can be generated using the scripts in the Bits of DNA GitHub repository):
1. In Figure 1 of their response, Patro et al. show an MA plot and state that “if it were true that these methods are ‘very very’ similar one would see most log-ratios close to 0 (within the red lines).” This is true. Below is the MA plot for kallisto with default parameters and Salmon with the –gcBias flag:
96.6% of the points lie within the red lines. Since this constitutes most of the points, it seems reasonable to conclude that the methods are indeed very very similar. When both programs are run in default mode, as I did in my blog post, 98.9% of the points lie within the red lines. Thus, using the criterion of Patro et al., the programs have very very similar, or near identical, output. These numbers are conservative, computed by omitting transcripts where both kallisto and Salmon determine that a transcript has zero abundance.
2. Furthermore, Patro et al. explain that their MA plot in Figure 1 “demonstrate[s] how deceiving count scatter plots can be in this particular context.” There is, superficially, some merit to this claim. The MA plot above looks like a smudge of points and seems at odds with the fact that 96.6% of the points lie within the red lines. However the plot displays 198,457 points corresponding to 198,457 quantified transcripts, and as a result many points obfuscate each other. The alpha parameter in ggplot2 sets the opacity/transparency of points, and should be used in such a case to reveal the density of points (see, e.g. Supplementary Figure 19 of Love et al. 2016). Below is a plot of the exact same points with alpha=0.01:
An R animation that interpolates between the two MA plots above shows the same points, with varying opacity parameters (alpha=1 -> 0.01) and helps to demonstrate how deceiving MA plots can be in this particular context:
3. The Patro et al. response fails to distinguish between two different comparisons I made in my blog post: (1) comparisons of default kallisto to default Salmon, and (2) default kallisto to Salmon with the –gcBias option. Comparisons of the programs with default options is important because with those options their output is near identical, and, as I explain in my blog post, this is not some cosmic coincidence but a result of Salmon directly implementing the key ideas of pseudoalignment. The Patro et al. 2017 paper is also not just about GC bias correction, as the authors claim in their response, but rather it is also “the Salmon paper” a descriptor that Patro et al. use 24 times in their response. Furthermore, when Patro et al. are asked about how to run Salmon they recommend running it with default options (see e.g. the epilogue below or the way Patro et al. run Salmon for analysis of the Bealieau-Jones-Greene described in #5) so that a comparison of the programs in default mode is of direct relevance to users.
In regards to the GC bias correction, Patro et al. 2017 claim in their abstract that “[GC bias correction] substantially improves the accuracy of abundance estimates and the sensitivity of subsequence differential expression analysis”. This is a general statement, not one about the sort of niche use-cases they describe in their response. The question then is whether Patro et al. provides support for this general statement and my argument has always been that it does not.
4. Patro et al. criticize my use of the ERR188140 sample to demonstrate how similar Salmon is to kallisto. They write that “the blog post author selected a single sample…”(boldface theirs) to claim that Salmon and kallisto produce output with “very very strong similarity (≃)” and raise the possibility that it was cherry picked, noting that “this particular sample has less GC-content bias” and marking it in a plot. I used ERR188140 because it was our sample of choice for many of the demonstrative analyses in the Bray et al. 2016 paper (see the kallisto paper analysis Github repository where the sample is mentioned since February 2016) and for that paper we had already generated the RSEM quantifications (and the alignments required for running the program), thus saving time in making the PCA analysis for my blogpost. ERR188140 was chosen for Bray et al. 2016 because it was the most deeply sequenced sample in the GEUVADIS dataset.
5. Contrary to the claim by Patro et al. in their response that I examined only one dataset, I also included in my post links with references to specific figures from four other papers that independently found that kallisto is near identical to Salmon. The fairest example for consideration is the additional analysis I mentioned of Beaulieu-Jones and Greene, and separately Patro, of the RNA-Seq dataset from Boj et al. 2015. With that analysis, there can be no claims of cherry-picking. The dataset was chosen by the authors of Beaulieu-Jones and Greene 2017, kallisto quantifications were produced by Beaulieu-Jones and Greene, and Salmon quantifications were prepared by Patro. Presumably the main author of the Salmon program ran Salmon with the best settings possible for the experiment. The fact that different individuals ran the programs is highlighted by the fact that they are not even based on identical annotations. They used different versions of RefSeq: Beaulieu-Jones and Greene quantified with 35,026 transcripts and Patro, who quantified later, used an annotation with 35,882 transcripts. There are eight samples in the analysis and MA plots, made by restricting the analysis to the transcripts in common, all look alike. As an example, the MA plot for SRR1654626 is:
The fraction of points within the red lines, calculated as before by omitting points at (0,0), is 98.6%. The Patro analysis of Bealieau-Greene was performed on March 8, 2017 with version 0.8.1 of Salmon, well after the –gcBias option was implemented, the Salmon (version 3 preprint describing the GC correction) published, and the paper submitted. The dates are verifiable in the GitHub repository with the Salmon results.
6. In arguing that kallisto and Salmon are different Patro et al. provide an interesting formula for the correlation for two random variables X and X+Y where X and Y are independent but its use in this context is a sleight of hand. The formula, which is a simple exercise for the reader to derive from the definition of correlation, is
It follows by Taylor series expansion that this is approximately
and if sd(X) is about 3.4 and sd(Y) about 0.5 (Patro et al.‘s numbers), then by inspection cor(X,X+Y) will be 0.99. In sample SRR1654626 shown above, when ignoring transcripts where both programs output 0, sd(X)=3.5 and sd(Y) = 0.43 which are fairly close to Patro et al.‘s numbers. However Patro et al. proceed with a non sequitur, writing that “this means that a substantial difference of 25% between reported counts is typical”. While the correlation formula makes no distributional assumptions, the 25% difference seems to be based on an assumption that Y is normally distributed. Specifically, if Y is normally distributed with mean 0 and standard deviation 0.5 then |Y| is half-normally distributed and a typical percent difference based on the median is
However the differences between kallisto and Salmon quantifications are far from normally distributed. The plot below shows the distribution of the differences between log2 counts of kallisto and salmon (again excluding cases where both programs output 0):
The blue vertical line is positioned at the median, which is at 0.001433093. This means that the typical difference between reported counts is not 25% but rather 0.1%.
7. In their response, Patro et al. highlight the recent Zhang et al. 2017 paper that benchmarked a number of RNA-Seq programs, including kallisto and Salmon. Patro et al. comment on a high correlation between a mode of Salmon that quantifies based with transcriptome alignments and RSEM. First, the correlations reported by Zhang et al. are Pearson correlations, and not Spearman correlations that I focused on in my blog post. Second, the alignment mode of Salmon has nothing to do with pseudoalignment, in that read alignments (in the case of Zhang et al. 2017 produced with STAR) are quantified directly, in a workflow the same as that of RSEM. Investigation of the similarities between alignment Salmon and RSEM that led to the high correlation is beyond the scope of this post. Finally, in discussing the similarities between programs the authors (Zhang et al.) write “Salmon, Sailfish and Kallisto, cluster tightly together with R 2 > 0.96.”
8. In regards to the EM algorithm, Patro et al. acknowledge that Salmon uses kallisto’s termination criteria and have updated their code to reflect this fact. I thank them for doing so, however this portion of their response is bizarre:
“What if Salmon executed more iterations of its offline phase and outperformed kallisto? Then its improvement could be attributed to the extra iterations instead of the different model, bias correction, or online phase. By using the same termination criteria for the offline phase of Salmon, we eliminate a confounding variable in the analysis.”
If Salmon could perform better by executing more iterations of the EM algorithm it should certainly do so. This is because parameters hard-wired in the code should be set in a way that provides users with the best possible performance.
9. At one point in their response Patro et al. write that “It is expected that Salmon, without the GC bias correction feature, will be similar to kallisto”, essentially conceding that default Salmon 
As explained in my post on How not to perform a differential expression analysis the reason that Love et al. recommend a DESeq2 workflow instead of a t-test for differential expression is because of the importance of regularizing variance estimates. This is made clear by repeating Patro et al.‘s GEUVADIS experiment with a typical three replicates per condition instead of eight:
With the t-test of transcripts Salmon cannot even achieve an FDR of less than 0.05.
10. Patro et al. find that switching to their recommended workflow (i.e. replacing the t-test with their own DESeq2) alters the difference between kallisto and Salmon at an FDR of 0.01 from 353% to 32%. Patro et al. describe this difference, in boldface, as “The results remain similar to the original published results when run using the accuser’s suggested pipeline.” Note that Patro et al. refer to a typical difference of 0.1% between counts generated by kallisto and Salmon as “not very very similar” (point #6) while insisting that 353% and 32% are “similar.”
11. The reanalysis of the GEUVADIS differential expression experiment by Patro et al. also fails to address one of the most important critiques in my blogpost, namely that a typical experimental design will not deliberately confound bias with condition. The plot below shows the difference between kallisto and Salmon in a typical experiment (3 replicates in each condition) followed by Love et al.’s recommended workflow (tximport -> DESeq2):
There is no apparent difference between kallisto and Salmon. Note that the samples in this experiment have the same GC bias as in Patro et al. 2017, the only difference being that samples are chosen randomly in a way that they are not confounded by batch. The lack of any observed difference in results between default kallisto and Salmon with the –gcBias option are the same with an 8×8 analysis:
There is no apparent difference between kallisto and Salmon, even though the simulation includes the same GC bias levels as in Patro et al. 2017 (just not confounded with condition) .
12. It is interesting to compare the 8×8 unconfounded experiment with the 8×8 confounded experiment.
While Salmon does improve on kallisto (although as discussed in point #10 the improvement is not 353% but rather 32% at an FDR of 0.01), the improvement in accuracy when performing an unconfounded experiment highlights why confounded experiments should not be performed in the first place.
13. Patro et al. claim that despite best intentions, “confounding of technical artifacts such as GC dependence with the biological comparison of interest does occur” and cite Gilad and Mizrahi-Man 2015. However the message of the Gilad and Mizrahi-Man paper is not that we must do our best to analyze confounded experiments. Rather, it is that with confounded experiments one may learn nothing at all. What they say is “In summary, we believe that our reanalysis indicates that the conclusions of the Mouse ENCODE Consortium papers pertaining to the clustering of the comparative gene expression data are unwarranted.” In other words, confounding of batch effect with variables of interest can render experiments worthless.
14. In response to my claim that GC bias has been reduced during the past 5 years, Patro et al. state:
A more informed assumption is that GC bias in sequencing data originates with PCR amplification and depends on thermocycler ramp speed (see, for example, Aird (2011) or t’ Hoen (2013)), and not from sequencing machines or reverse transcription protocols which may have improved in the past 5 years.
This statement is curious in that it seems to assume that, unlike sequencing machines or reverse transcription protocols, PCR amplification and thermocycler technology could not have improved in the past 5 years. As an example to the contrary, consider that just months before the publication of the GEUVADIS data, New England Biolabs released a new polymerase which claimed to address this very issue. GC bias is a ubiquitous issue in molecular biology and of course there are ongoing efforts to address it in the wet lab. Furthermore, continued research and benchmarking aimed at reducing GC bias, (see e.g. Thorner et al. 2014) have led to marked improvements in library quality and standardization of experiments across labs. Anyone who performs bulk RNA-Seq, as we do in my lab, knows that RNA-Seq is no longer an ad hoc experiment.
15. Patro et al. write that
The point of the simulation was to demonstrate that, while modeling fragment sequence bias reduces gross mis-estimation (false reports of isoform switching across labs in real data — see for example Salmon Supplementary Figure 5 showing GEUVADIS data), the bias modeling does not lead to overall loss of signal. Consider that one could reduce false positives simply by attenuating signal or adding noise to all transcript abundances.
However none of the simulations or results in Patro et al. 2017 address the question of whether bias modeling leads to overall loss of signal. To answer it would require examining the true and false positives in a comparison of default Salmon and Salmon with –gcBias. Not only did Patro et al. not do the relevant intra-program comparisons, they did inter-program comparisons instead which clearly bear no relevance to the point they now claim they were making.
16. I want to make very clear that I believe that GC bias correction during RNA-Seq quantification is valuable and I agree with Patro et al. that it can be important for meta-analyses, especially of the kind that take place by large genome consortia. One of the interesting results in Patro et al. is the SEQC analysis (Supplementary Figure 4) which shows that that Salmon is more consistent in intra-center quantification in one sample (HBRR). However in a second experiment (UHRR) the programs are near identical in their quantification differences within and between centers and based on the results shown above I don’t believe that Patro et al. 2017 achieves its stated aim of showing that GC correction has an effect on typical differential analyses experiments that utilize typical downstream analyses.
17. I showed the results of running kallisto in default mode and Salmon with GC bias correction on a well-studied dataset from Trapnell et al. 2013. Patro et al. claim they were unable to reproduce my results, but that is because they performed a transcript level analysis despite the fact that I made it very clear in my post that I performed a gene level analysis. I chose to show results at the gene level to draw a contrast with Figure 3c of Trapnell et al. 2013. The results of Patro et al. at the transcript level show that even then the extent of overlap is remarkable. These results are consistent with the simulation results (see point #11).
18. The Salmon authors double down on their runtime analysis by claiming that “The running time discussion presented in the Salmon paper is accurate.” This is difficult to reconcile with two facts
(a) According to Patro et al.’s rebuttal “kallisto is faster when using a small number of threads” yet this was not presented in Patro et al. 2017.
(b) According to Patro et al. (see, e.g., the Salmon program GitHub), when running kallisto or Salmon with 30 threads what is being benchmarked is disk I/O and not the runtime of the programs.
If Patro et al. agree that to benchmark the speed of a program one must use a small number of threads, and Patro et al. agree that with a small number of threads kallisto is faster, then the only possible conclusion is that the running time discussion presented in the Salmon paper is not accurate.
19. The Patro et al. response has an entire section (3.1) devoted to explaining why quasimapping (used by Salmon) is distinct from pseudoalignment (introduced in the kallisto paper). Patro et al. describe quasimapping as “a different algorithm, different data structure, and computes different results.” Furthermore, in a blog post, Patro explained that RapMap (on which Salmon is based) implements both quasimapping and pseudoalignment, and that these are distinct concepts. He writes specifically that in contrast to the first algorithm provided by RapMap (pseudoalignment), “the second algorithm provided by RapMap — quasi-mapping — is a novel one”.
One of the reviewers of the Salmon paper recently published his review, which begins with the sentence “The authors present salmon, a new RNAseq quantification tool that uses pseudoalignment…” This directly contradicts the assertion of Patro et al. that quasimapping is “a different algorithm, different data structure” or that quasimapping is novel. In my blog post I provided a detailed walk-through that affirms that the reviewer is right. I showed how the quasimapping underlying Salmon is literally acting in identical ways on the k-mers in reads. Moreover, the results above show that Salmon, using quasimapping, does not “compute different results”. Unsurprisingly, its output is near identical to kallisto.
20. Patro et al. write that “The title of Sailfish paper contains the words ‘alignment-free’, which indicates that it was Sailfish that first presented the key idea of abandoning alignment. The term alignment-free has a long history in genomics and is used to describe methods in which the information inherent in a complete read is discarded in favor of the direct use of it’s substrings. Sailfish is indeed an alignment-free method because it shreds reads into constituent k-mers, and those are then operated on without regard to which read they originated from. The paper is aptly titled. The concept of pseudoalignment is distinct in that complete reads are associated to targets, even if base-pair alignments are not described.
21. Patro et al. write that “Salmon, including many of its main ideas, was widely known in the field prior to the kallisto preprint.” and mention that Zhang et al. 2015 included a brief description of Salmon. Zhang et al. 2015 was published on June 5, 2015, a month after the kallisto preprint was published, and its description of Salmon, though brief, was the first available for the program. Nowhere else, prior to the Zhang et al. publication, was there any description of what Salmon does or how it works, even at a high-level.
Notably, the paragraph on Salmon of Zhang et al. shows that Salmon, in its initial form, had nothing to do with pseudoalignment:
“Salmon is based on a novel lightweight alignment model that uses chains of maximal exact matches between sequencing fragments and reference transcripts to determine the potential origin of RNA‐seq reads.”
This is consistent with the PCA plot of my blog post which shows that initial versions of Salmon were very different from kallisto, and that Salmon
22. My blogpost elicited an intense discussion in the comments and on social media of whether Patro et al. adequately attributed key ideas of Salmon to kallisto. Patro et al. They did not.
Patro et al. reference numerous citations to kallisto in Patro et al. 2017 which I’ve reproduced below
Only two of these references attribute any aspect of Salmon to kallisto. One of them, the Salmon bootstrap, is described as “inspired by kallisto” (in fact it is identical to that of kallisto). There is only one citation in Salmon to the key idea that has made it near identical to kallisto, namely the use of pseudoalignment, and that is to the RapMap paper from the Patro group (Srivastava et al. 2016).
Despite boasting of a commitment to open source principles and embracing preprints, Patro et al. conveniently ignore the RapMap preprints (Srivastava et al. 2015). Despite many mentions of kallisto, none of the four versions of the preprint acknowledge the direct use of the ideas in Bray et al. 2016 in any way, shape or form. The intent of Srivastava et al. is very clear. In the journal version the authors still do not acknowledge that “quasi mapping” is just pseudoalignment implemented with a suffix array, instead using words such as “inspired” and “motivated” to obfuscate the truth. Wording matters.
Epilogue
Discussion of the Zhang et al. 2017 paper by Patro et al., along with a tweet by Lappalainen about programs not giving identical results lead me to look more deeply into the Zhang et al. 2017 paper.
The exploration turned out to be interesting. On the one hand, some figures in Zhang et al. 2017 contradict Lappalainen’s claim that “none of the methods seem to give identical results…”. For example, Figure S4 from the paper shows quantifications for four genes where kallisto and Salmon produce near identical results.
On the other hand, Figure 7 from the paper is an example from a simulation on a single gene where kallisto performed very differently from Salmon:
I contacted the authors to find out how they ran kallisto and Salmon. It turns out that for all the results in the paper with the exception of Figure 7, the programs were run as follows:
· kallisto quant -i $KAL_INDEX –fr-stranded –plaintext $DATADIR/${f}_1.fq $DATADIR/${f}_2.fq -t 8 -o ./kallisto/
· salmon quant -i $SALMON_INDEX -l ISF -1 $DATADIR/${f}_1.fq -2 $DATADIR/${f}_2.fq -p 8 -o salmon_em –incompatPrior 0
We then exchanged some further emails, after which they sent the data (reads) for the figure, we ran kallisto on our end and found discordant results with what was reported in the paper, they re-ran kallisto on their end, and after these exchanges we converged to an updated (and corrected) figure which shows Sailfish
Note that kallisto is near identical in performance to Sailfish, which I explained in my blog post about Salmon has also converged to kallisto. However Salmon is different.
It turned out that for this one figure, Salmon was run with a non-standard set of options, specifically with the additional option –numPreAuxModelSamples 0 (although notably Patro did not recommend using the –gcBias option). The recommendation to run with this option was made by Patro to Zhang et al. after they contacted him early in January 2017 to ask for the best way to run Salmon for the experiment. What the flag does is turn off the online phase of Salmon (hence the 0 in –numPreAuxModelSamples 0) that is used to initially estimate the fragment length distribution. There is a good rationale for using the flag, namely the very small number of reads in the simulation makes it impossible to accurately learn auxiliary parameters as one might with a full dataset. However on January 13th, Patro changed the behavior of the option in a way that allowed Salmon to optimize for the specific experiment at hand. The default fragment length distribution in Salmon had been set the same as that in Cufflinks (mean 200, standard deviation 80). These settings match typical experimental data, and were chosen by Cole Trapnell and myself after examining numerous biological datasets. Setting –numPreAuxModelSamples to 0 forced Salmon to use those parameters. However on January 13th Patro changed the defaults in Salmon to mean = 250 and standard deviation = 25. The numbers 250 and 25 are precisely the defaults for the polyester program that simulates reads. Polyester (with default parameters) is what Zhang et al. 2017 used to simulate reads for Figure 7.
Zhang et al. also contacted me on January 9th and I did not reply to their email. I had just moved institutions (from UC Berkeley to Caltech) on January 1st, and did not have the time to investigate in detail the issues they raised. I thank them for being forthcoming and helpful in reviewing Figure 7 post publication.
Returning to Lappalainen’s comment, it is true that Salmon results are different from kallisto in Figure 7 and one reason may be that Patro hard wired parameters for a flag that was used to match the parameters of the simulation. With the exception of that figure, throughout the paper Salmon
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