Model and normalization

The starting point of a DESeq2 analysis is a count matrix K with one row for each gene i and one column for each sample j. The matrix entries K _ij indicate the number of sequencing reads that have been unambiguously mapped to a gene in a sample. Note that although we refer in this paper to counts of reads in genes, the methods presented here can be applied as well to other kinds of HTS count data. For each gene, we fit a generalized linear model (GLM) [12] as follows.

We model read counts K _ij as following a negative binomial distribution (sometimes also called a gamma-Poisson distribution) with mean μ _ij and dispersion α _i . The mean is taken as a quantity q _ij , proportional to the concentration of cDNA fragments from the gene in the sample, scaled by a normalization factor s _ij , i.e., μ _ij =s _ij q _ij . For many applications, the same constant s _j can be used for all genes in a sample, which then accounts for differences in sequencing depth between samples. To estimate these size factors, the DESeq2 package offers the median-of-ratios method already used in DESeq [4]. However, it can be advantageous to calculate gene-specific normalization factors s _ij to account for further sources of technical biases such as differing dependence on GC content, gene length or the like, using published methods [13],[14], and these can be supplied instead.

We use GLMs with a logarithmic link, $\underset{2}{log}{q}_{\mathit{\text{ij}}}=\sum _r{x}_{\mathit{\text{jr}}}{\beta }_{\mathit{\text{ir}}}$, with design matrix elements x _jr and coefficients β _ir . In the simplest case of a comparison between two groups, such as treated and control samples, the design matrix elements indicate whether a sample j is treated or not, and the GLM fit returns coefficients indicating the overall expression strength of the gene and the log ₂ fold change between treatment and control. The use of linear models, however, provides the flexibility to also analyze more complex designs, as is often useful in genomic studies [15].

Empirical Bayes shrinkage for dispersion estimation

Within-group variability, i.e., the variability between replicates, is modeled by the dispersion parameter α _i , which describes the variance of counts via $Var{K}_{\mathit{\text{ij}}}={\mu }_{\mathit{\text{ij}}}+{\alpha }_i{\mu }_{\mathit{\text{ij}}}^2$. Accurate estimation of the dispersion parameter α _i is critical for the statistical inference of differential expression. For studies with large sample sizes this is usually not a problem. For controlled experiments, however, sample sizes tend to be smaller (experimental designs with as little as two or three replicates are common and reasonable), resulting in highly variable dispersion estimates for each gene. If used directly, these noisy estimates would compromise the accuracy of differential expression testing.

One sensible solution is to share information across genes. In DESeq2, we assume that genes of similar average expression strength have similar dispersion. We here explain the concepts of our approach using as examples a dataset by Bottomly et al. [16] with RNA-seq data for mice of two different strains and a dataset by Pickrell et al. [17] with RNA-seq data for human lymphoblastoid cell lines. For the mathematical details, see Materials and methods.

We first treat each gene separately and estimate gene-wise dispersion estimates (using maximum likelihood), which rely only on the data of each individual gene (black dots in Figure 1). Next, we determine the location parameter of the distribution of these estimates; to allow for dependence on average expression strength, we fit a smooth curve, as shown by the red line in Figure 1. This provides an accurate estimate for the expected dispersion value for genes of a given expression strength but does not represent deviations of individual genes from this overall trend. We then shrink the gene-wise dispersion estimates toward the values predicted by the curve to obtain final dispersion values (blue arrow heads). We use an empirical Bayes approach (Materials and methods), which lets the strength of shrinkage depend (i) on an estimate of how close true dispersion values tend to be to the fit and (ii) on the degrees of freedom: as the sample size increases, the shrinkage decreases in strength, and eventually becomes negligible. Our approach therefore accounts for gene-specific variation to the extent that the data provide this information, while the fitted curve aids estimation and testing in less information-rich settings.

Our approach is similar to the one used by DSS [6], in that both methods sequentially estimate a prior distribution for the true dispersion values around the fit, and then provide the maximum a posteriori (MAP) as the final estimate. It differs from the previous implementation of DESeq, which used the maximum of the fitted curve and the gene-wise dispersion estimate as the final estimate and tended to overestimate the dispersions (Additional file 1: Figure S2). The approach of DESeq2 differs from that of edgeR [3], as DESeq2 estimates the width of the prior distribution from the data and therefore automatically controls the amount of shrinkage based on the observed properties of the data. In contrast, the default steps in edgeR require a user-adjustable parameter, the prior degrees of freedom, which weighs the contribution of the individual gene estimate and edgeR’s dispersion fit.

Note that in Figure 1 a number of genes with gene-wise dispersion estimates below the curve have their final estimates raised substantially. The shrinkage procedure thereby helps avoid potential false positives, which can result from underestimates of dispersion. If, on the other hand, an individual gene’s dispersion is far above the distribution of the gene-wise dispersion estimates of other genes, then the shrinkage would lead to a greatly reduced final estimate of dispersion. We reasoned that in many cases, the reason for extraordinarily high dispersion of a gene is that it does not obey our modeling assumptions; some genes may show much higher variability than others for biological or technical reasons, even though they have the same average expression levels. In these cases, inference based on the shrunken dispersion estimates could lead to undesirable false positive calls. DESeq2 handles these cases by using the gene-wise estimate instead of the shrunken estimate when the former is more than 2 residual standard deviations above the curve.

Empirical Bayes shrinkage for fold-change estimation

A common difficulty in the analysis of HTS data is the strong variance of LFC estimates for genes with low read count. We demonstrate this issue using the dataset by Bottomly et al. [16]. As visualized in Figure 2A, weakly expressed genes seem to show much stronger differences between the compared mouse strains than strongly expressed genes. This phenomenon, seen in most HTS datasets, is a direct consequence of dealing with count data, in which ratios are inherently noisier when counts are low. This heteroskedasticity (variance of LFCs depending on mean count) complicates downstream analysis and data interpretation, as it makes effect sizes difficult to compare across the dynamic range of the data.

DESeq2 overcomes this issue by shrinking LFC estimates toward zero in a manner such that shrinkage is stronger when the available information for a gene is low, which may be because counts are low, dispersion is high or there are few degrees of freedom. We again employ an empirical Bayes procedure: we first perform ordinary GLM fits to obtain maximum-likelihood estimates (MLEs) for the LFCs and then fit a zero-centered normal distribution to the observed distribution of MLEs over all genes. This distribution is used as a prior on LFCs in a second round of GLM fits, and the MAP estimates are kept as final estimates of LFC. Furthermore, a standard error for each estimate is reported, which is derived from the posterior’s curvature at its maximum (see Materials and methods for details). These shrunken LFCs and their standard errors are used in the Wald tests for differential expression described in the next section.

The resulting MAP LFCs are biased toward zero in a manner that removes the problem of exaggerated LFCs for low counts. As Figure 2B shows, the strongest LFCs are no longer exhibited by genes with weakest expression. Rather, the estimates are more evenly spread around zero, and for very weakly expressed genes (with less than one read per sample on average), LFCs hardly deviate from zero, reflecting that accurate LFC estimates are not possible here.

The strength of shrinkage does not depend simply on the mean count, but rather on the amount of information available for the fold change estimation (as indicated by the observed Fisher information; see Materials and methods). Two genes with equal expression strength but different dispersions will experience a different amount of shrinkage (Figure 2C,D). The shrinkage of LFC estimates can be described as a bias-variance trade-off [18]: for genes with little information for LFC estimation, a reduction of the strong variance is bought at the cost of accepting a bias toward zero, and this can result in an overall reduction in mean squared error, e.g., when comparing to LFC estimates from a new dataset. Genes with high information for LFC estimation will have, in our approach, LFCs with both low bias and low variance. Furthermore, as the degrees of freedom increase, and the experiment provides more information for LFC estimation, the shrunken estimates will converge to the unshrunken estimates. We note that other Bayesian efforts toward moderating fold changes for RNA-seq include hierarchical models [8],[19] and the GFOLD (or generalized fold change) tool [20], which uses a posterior distribution of LFCs.

The shrunken MAP LFCs offer a more reproducible quantification of transcriptional differences than standard MLE LFCs. To demonstrate this, we split the Bottomly et al. samples equally into two groups, I and II, such that each group contained a balanced split of the strains, simulating a scenario where an experiment (samples in group I) is performed, analyzed and reported, and then independently replicated (samples in group II). Within each group, we estimated LFCs between the strains and compared between groups I and II, using the MLE LFCs (Figure 3A) and using the MAP LFCs (Figure 3B). Because the shrinkage moves large LFCs that are not well supported by the data toward zero, the agreement between the two independent sample groups increases considerably. Therefore, shrunken fold-change estimates offer a more reliable basis for quantitative conclusions than normal MLEs.

This makes shrunken LFCs also suitable for ranking genes, e.g., to prioritize them for follow-up experiments. For example, if we sort the genes in the two sample groups of Figure 3 by unshrunken LFC estimates, and consider the 100 genes with the strongest up- or down-regulation in group I, we find only 21 of these again among the top 100 up- or down-regulated genes in group II. However, if we rank the genes by shrunken LFC estimates, the overlap improves to 81 of 100 genes (Additional file 1: Figure S3).

A simpler often used method is to add a fixed number (pseudocount) to all counts before forming ratios. However, this requires the choice of a tuning parameter and only reacts to one of the sources of uncertainty, low counts, but not to gene-specific dispersion differences or sample size. We demonstrate this in the Benchmarks section below.

Hypothesis tests for differential expression

After GLMs are fit for each gene, one may test whether each model coefficient differs significantly from zero. DESeq2 reports the standard error for each shrunken LFC estimate, obtained from the curvature of the coefficient’s posterior (dashed lines in Figure 2D) at its maximum. For significance testing, DESeq2 uses a Wald test: the shrunken estimate of LFC is divided by its standard error, resulting in a z-statistic, which is compared to a standard normal distribution. (See Materials and methods for details.) The Wald test allows testing of individual coefficients, or contrasts of coefficients, without the need to fit a reduced model as with the likelihood ratio test, though the likelihood ratio test is also available as an option in DESeq2. The Wald test P values from the subset of genes that pass an independent filtering step, described in the next section, are adjusted for multiple testing using the procedure of Benjamini and Hochberg [21].

Automatic independent filtering

Due to the large number of tests performed in the analysis of RNA-seq and other genome-wide experiments, the multiple testing problem needs to be addressed. A popular objective is control or estimation of the FDR. Multiple testing adjustment tends to be associated with a loss of power, in the sense that the FDR for a set of genes is often higher than the individual P values of these genes. However, the loss can be reduced if genes that have little or no chance of being detected as differentially expressed are omitted from the testing, provided that the criterion for omission is independent of the test statistic under the null hypothesis [22] (see Materials and methods). DESeq2 uses the average expression strength of each gene, across all samples, as its filter criterion, and it omits all genes with mean normalized counts below a filtering threshold from multiple testing adjustment. DESeq2 by default will choose a threshold that maximizes the number of genes found at a user-specified target FDR. In Figures 2A,B and 3, genes found in this way to be significant at an estimated FDR of 10% are depicted in red. Depending on the distribution of the mean normalized counts, the resulting increase in power can be substantial, sometimes making the difference in whether or not any differentially expressed genes are detected.

Hypothesis tests with thresholds on effect size

Specifying minimum effect size

Most approaches to testing for differential expression, including the default approach of DESeq2, test against the null hypothesis of zero LFC. However, if any biological processes are genuinely affected by the difference in experimental treatment, this null hypothesis implies that the gene under consideration is perfectly decoupled from these processes. Due to the high interconnectedness of cells’ regulatory networks, this hypothesis is, in fact, implausible, and arguably wrong for many if not most genes. Consequently, with sufficient sample size, even genes with a very small but non-zero LFC will eventually be detected as differentially expressed. A change should therefore be of sufficient magnitude to be considered biologically significant. For small-scale experiments, statistical significance is often a much stricter requirement than biological significance, thereby relieving the researcher from the need to decide on a threshold for biological significance.

For well-powered experiments, however, a statistical test against the conventional null hypothesis of zero LFC may report genes with statistically significant changes that are so weak in effect strength that they could be considered irrelevant or distracting. A common procedure is to disregard genes whose estimated LFC β _ir is below some threshold, |β _ir |≤θ. However, this approach loses the benefit of an easily interpretable FDR, as the reported P value and adjusted P value still correspond to the test of zero LFC. It is therefore desirable to include the threshold in the statistical testing procedure directly, i.e., not to filter post hoc on a reported fold-change estimate, but rather to evaluate statistically directly whether there is sufficient evidence that the LFC is above the chosen threshold.

DESeq2 offers tests for composite null hypotheses of the form |β _ir |≤θ, where β _ir is the shrunken LFC from the estimation procedure described above. (See Materials and methods for details.) Figure 4A demonstrates how such a thresholded test gives rise to a curved decision boundary: to reach significance, the estimated LFC has to exceed the specified threshold by an amount that depends on the available information. We note that related approaches to generate gene lists that satisfy both statistical and biological significance criteria have been previously discussed for microarray data [23] and recently for sequencing data [19].

Detection of count outliers

Parametric methods for detecting differential expression can have gene-wise estimates of LFC overly influenced by individual outliers that do not fit the distributional assumptions of the model [24]. An example of such an outlier would be a gene with single-digit counts for all samples, except one sample with a count in the thousands. As the aim of differential expression analysis is typically to find consistently up- or down-regulated genes, it is useful to consider diagnostics for detecting individual observations that overly influence the LFC estimate and P value for a gene. A standard outlier diagnostic is Cook’s distance [25], which is defined within each gene for each sample as the scaled distance that the coefficient vector, ${\overrightarrow{\beta }}_i$, of a linear model or GLM would move if the sample were removed and the model refit.

DESeq2 flags, for each gene, those samples that have a Cook’s distance greater than the 0.99 quantile of the F(p,m−p) distribution, where p is the number of model parameters including the intercept, and m is the number of samples. The use of the F distribution is motivated by the heuristic reasoning that removing a single sample should not move the vector ${\overrightarrow{\beta }}_i$ outside of a 99% confidence region around ${\overrightarrow{\beta }}_i$ fit using all the samples [25]. However, if there are two or fewer replicates for a condition, these samples do not contribute to outlier detection, as there are insufficient replicates to determine outlier status.

How should one deal with flagged outliers? In an experiment with many replicates, discarding the outlier and proceeding with the remaining data might make best use of the available data. In a small experiment with few samples, however, the presence of an outlier can impair inference regarding the affected gene, and merely ignoring the outlier may even be considered data cherry-picking – and therefore, it is more prudent to exclude the whole gene from downstream analysis.

Hence, DESeq2 offers two possible responses to flagged outliers. By default, outliers in conditions with six or fewer replicates cause the whole gene to be flagged and removed from subsequent analysis, including P value adjustment for multiple testing. For conditions that contain seven or more replicates, DESeq2 replaces the outlier counts with an imputed value, namely the trimmed mean over all samples, scaled by the size factor, and then re-estimates the dispersion, LFCs and P values for these genes. As the outlier is replaced with the value predicted by the null hypothesis of no differential expression, this is a more conservative choice than simply omitting the outlier. When there are many degrees of freedom, the second approach avoids discarding genes that might contain true differential expression.

Additional file 1: Figure S4 displays the outlier replacement procedure for a single gene in a seven by seven comparison of the Bottomly et al. [16] dataset. While the original fitted means are heavily influenced by a single sample with a large count, the corrected LFCs provide a better fit to the majority of the samples.

Regularized logarithm transformation

For certain analyses, it is useful to transform data to render them homoskedastic. As an example, consider the task of assessing sample similarities in an unsupervised manner using a clustering or ordination algorithm. For RNA-seq data, the problem of heteroskedasticity arises: if the data are given to such an algorithm on the original count scale, the result will be dominated by highly expressed, highly variable genes; if logarithm-transformed data are used, undue weight will be given to weakly expressed genes, which show exaggerated LFCs, as discussed above. Therefore, we use the shrinkage approach of DESeq2 to implement a regularized logarithm transformation (rlog), which behaves similarly to a log2 transformation for genes with high counts, while shrinking together the values for different samples for genes with low counts. It therefore avoids a commonly observed property of the standard logarithm transformation, the spreading apart of data for genes with low counts, where random noise is likely to dominate any biologically meaningful signal. When we consider the variance of each gene, computed across samples, these variances are stabilized – i.e., approximately the same, or homoskedastic – after the rlog transformation, while they would otherwise strongly depend on the mean counts. It thus facilitates multivariate visualization and ordinations such as clustering or principal component analysis that tend to work best when the variables have similar dynamic range. Note that while the rlog transformation builds upon on our LFC shrinkage approach, it is distinct from and not part of the statistical inference procedure for differential expression analysis described above, which employs the raw counts, not transformed data.

The rlog transformation is calculated by fitting for each gene a GLM with a baseline expression (i.e., intercept only) and, computing for each sample, shrunken LFCs with respect to the baseline, using the same empirical Bayes procedure as before (Materials and methods). Here, however, the sample covariate information (e.g. treatment or control) is not used, so that all samples are treated equally. The rlog transformation accounts for variation in sequencing depth across samples as it represents the logarithm of q _ij after accounting for the size factors s _ij . This is in contrast to the variance-stabilizing transformation (VST) for overdispersed counts introduced in DESeq [4]: while the VST is also effective at stabilizing variance, it does not directly take into account differences in size factors; and in datasets with large variation in sequencing depth (dynamic range of size factors $\gtrsim$4) we observed undesirable artifacts in the performance of the VST. A disadvantage of the rlog transformation with respect to the VST is, however, that the ordering of genes within a sample will change if neighboring genes undergo shrinkage of different strength. As with the VST, the value of rlog(K _ij ) for large counts is approximately equal to log2(K _ij /s _j ). Both the rlog transformation and the VST are provided in the DESeq2 package.

We demonstrate the use of the rlog transformation on the RNA-seq dataset of Hammer et al. [26], wherein RNA was sequenced from the dorsal root ganglion of rats that had undergone spinal nerve ligation and controls, at 2 weeks and at 2 months after the ligation. The count matrix for this dataset was downloaded from the ReCount online resource [27]. This dataset offers more subtle differences between conditions than the Bottomly et al. [16] dataset. Figure 5 provides diagnostic plots of the normalized counts under the ordinary logarithm with a pseudocount of 1 and the rlog transformation, showing that the rlog both stabilizes the variance through the range of the mean of counts and helps to find meaningful patterns in the data.

Gene-level analysis

We here present DESeq2 for the analysis of per-gene counts, i.e., the total number of reads that can be uniquely assigned to a gene. In contrast, several algorithms [28],[29] work with probabilistic assignments of reads to transcripts, where multiple, overlapping transcripts can originate from each gene. It has been noted that the total read count approach can result in false detection of differential expression when in fact only transcript isoform lengths change, and even in a wrong sign of LFCs in extreme cases [28]. However, in our benchmark, discussed in the following section, we found that LFC sign disagreements between total read count and probabilistic-assignment-based methods were rare for genes that were differentially expressed according to either method (Additional file 1: Figure S5). Furthermore, if estimates for average transcript length are available for the conditions, these can be incorporated into the DESeq2 framework as gene- and sample-specific normalization factors. In addition, the approach used in DESeq2 can be extended to isoform-specific analysis, either through generalized linear modeling at the exon level with a gene-specific mean as in the DEXSeq package [30] or through counting evidence for alternative isoforms in splice graphs [31],[32]. In fact, the latest release version of DEXSeq now uses DESeq2 as its inferential engine and so offers shrinkage estimation of dispersion and effect sizes for an exon-level analysis, too.

Comparative benchmarks

To assess how well DESeq2 performs for standard analyses in comparison to other current methods, we used a combination of simulations and real data. The negative-binomial-based approaches compared were DESeq (old) [4], edgeR [33], edgeR with the robust option [34], DSS [6] and EBSeq [35]. Other methods compared were the voom normalization method followed by linear modeling using the limma package [36] and the SAMseq permutation method of the samr package [24]. For the benchmarks using real data, the Cuffdiff 2 [28] method of the Cufflinks suite was included. For version numbers of the software used, see Additional file 1: Table S3. For all algorithms returning P values, the P values from genes with non-zero sum of read counts across samples were adjusted using the Benjamini–Hochberg procedure [21].

Benchmarks through simulation

Sensitivity and precision We simulated datasets of 10,000 genes with negative binomial distributed counts. To simulate data with realistic moments, the mean and dispersions were drawn from the joint distribution of means and gene-wise dispersion estimates from the Pickrell et al. data, fitting only an intercept term. These datasets were of varying total sample size (m∈{6,8,10,20}), and the samples were split into two equal-sized groups; 80% of the simulated genes had no true differential expression, while for 20% of the genes, true fold changes of 2, 3 and 4 were used to generate counts across the two groups, with the direction of fold change chosen randomly. The simulated differentially expressed genes were chosen uniformly at random among all the genes, throughout the range of mean counts. MA-plots of the true fold changes used in the simulation and the observed fold changes induced by the simulation for one of the simulation settings are shown in Additional file 1: Figure S6.

Algorithms’ performance in the simulation benchmark was assessed by their sensitivity and precision. The sensitivity was calculated as the fraction of genes with adjusted P value <0.1 among the genes with true differences between group means. The precision was calculated as the fraction of genes with true differences between group means among those with adjusted P value <0.1. The sensitivity is plotted over 1−precision, or the FDR, in Figure 6. DESeq2, and also edgeR, often had the highest sensitivity of the algorithms that controlled type-I error in the sense that the actual FDR was at or below 0.1, the threshold for adjusted P values used for calling differentially expressed genes. DESeq2 had higher sensitivity compared to the other algorithms, particularly for small fold change (2 or 3), as was also found in benchmarks performed by Zhou et al. [34]. For larger sample sizes and larger fold changes the performance of the various algorithms was more consistent.

The overly conservative calling of the old DESeq tool can be observed, with reduced sensitivity compared to the other algorithms and an actual FDR less than the nominal value of 0.1. We note that EBSeq version 1.4.0 by default removes low-count genes – whose 75% quantile of normalized counts is less than ten – before calling differential expression. The sensitivity of algorithms on the simulated data across a range of the mean of counts are more closely compared in Additional file 1: Figure S9.

Outlier sensitivity We used simulations to compare the sensitivity and specificity of DESeq2’s outlier handling approach to that of edgeR, which was recently added to the software and published while this manuscript was under review. edgeR now includes an optional method to handle outliers by iteratively refitting the GLM after down-weighting potential outlier counts [34]. The simulations, summarized in Additional file 1: Figure S10, indicated that both approaches to outliers nearly recover the performance on an outlier-free dataset, though edgeR-robust had slightly higher actual than nominal FDR, as seen in Additional file 1: Figure S11.

Precision of fold change estimates We benchmarked the DESeq2 approach of using an empirical prior to achieve shrinkage of LFC estimates against two competing approaches: the GFOLD method, which can analyze experiments without replication [20] and can also handle experiments with replicates, and the edgeR package, which provides a pseudocount-based shrinkage termed predictive LFCs. Results are summarized in Additional file 1: Figures S12–S16. DESeq2 had consistently low root-mean-square error and mean absolute error across a range of sample sizes and models for a distribution of true LFCs. GFOLD had similarly low error to DESeq2 over all genes; however, when focusing on differentially expressed genes, it performed worse for larger sample sizes. edgeR with default settings had similarly low error to DESeq2 when focusing only on the differentially expressed genes, but had higher error over all genes.

Clustering We compared the performance of the rlog transformation against other methods of transformation or distance calculation in the recovery of simulated clusters. The adjusted Rand index [37] was used to compare a hierarchical clustering based on various distances with the true cluster membership. We tested the Euclidean distance for normalized counts, logarithm of normalized counts plus a pseudocount of 1, rlog-transformed counts and VST counts. In addition we compared these Euclidean distances with the Poisson distance implemented in the PoiClaClu package [38], and a distance implemented internally in the plotMDS function of edgeR (though not the default distance, which is similar to the logarithm of normalized counts). The results, shown in Additional file 1: Figure S17, revealed that when the size factors were equal for all samples, the Poisson distance and the Euclidean distance of rlog-transformed or VST counts outperformed other methods. However, when the size factors were not equal across samples, the rlog approach generally outperformed the other methods. Finally, we note that the rlog transformation provides normalized data, which can be used for a variety of applications, of which distance calculation is one.

Benchmark for RNA sequencing data

While simulation is useful to verify how well an algorithm behaves with idealized theoretical data, and hence can verify that the algorithm performs as expected under its own assumptions, simulations cannot inform us how well the theory fits reality. With RNA-seq data, there is the complication of not knowing fully or directly the underlying truth; however, we can work around this limitation by using more indirect inference, explained below.

In the following benchmarks, we considered three performance metrics for differential expression calling: the false positive rate (or 1 minus the specificity), sensitivity and precision. We can obtain meaningful estimates of specificity from looking at datasets where we believe all genes fall under the null hypothesis of no differential expression [39]. Sensitivity and precision are more difficult to estimate, as they require independent knowledge of those genes that are differentially expressed. To circumvent this problem, we used experimental reproducibility on independent samples (though from the same dataset) as a proxy. We used a dataset with large numbers of replicates in both of two groups, where we expect that truly differentially expressed genes exist. We repeatedly split this dataset into an evaluation set and a larger verification set, and compared the calls from the evaluation set with the calls from the verification set, which were taken as truth. It is important to keep in mind that the calls from the verification set are only an approximation of the true differential state, and the approximation error has a systematic and a stochastic component. The stochastic error becomes small once the sample size of the verification set is large enough. For the systematic errors, our benchmark assumes that these affect all algorithms more or less equally and do not markedly change the ranking of the algorithms.

False positive rate To evaluate the false positive rate of the algorithms, we considered mock comparisons from a dataset with many samples and no known condition dividing the samples into distinct groups. We used the RNA-seq data of Pickrell et al. [17] for lymphoblastoid cell lines derived from unrelated Nigerian individuals. We chose a set of 26 RNA-seq samples of the same read length (46 base pairs) from male individuals. We randomly drew without replacement ten samples from the set to compare five against five, and this process was repeated 30 times. We estimated the false positive rate associated with a critical value of 0.01 by dividing the number of P values less than 0.01 by the total number of tests; genes with zero sum of read counts across samples were excluded. The results over the 30 replications, summarized in Figure 7, indicated that all algorithms generally controlled the number of false positives. DESeq (old) and Cuffdiff 2 appeared overly conservative in this analysis, not using up their type-I error budget.

Sensitivity To obtain an impression of the sensitivity of the algorithms, we considered the Bottomly et al. [16] dataset, which contains ten and eleven replicates of two different, genetically homogeneous mice strains. This allowed for a split of three vs three for the evaluation set and seven vs eight for the verification set, which were balanced across the three experimental batches. Random splits were replicated 30 times. Batch information was not provided to the DESeq (old), DESeq2, DSS, edgeR or voom algorithms, which can accommodate complex experimental designs, to have comparable calls across all algorithms.

We rotated though each algorithm to determine the calls of the verification set. For a given algorithm’s verification set calls, we tested the evaluation set calls of every algorithm. We used this approach rather than a consensus-based method, as we did not want to favor or disfavor any particular algorithm or group of algorithms. Sensitivity was calculated as in the simulation benchmark, now with true differential expression defined by an adjusted P value <0.1 in the larger verification set, as diagrammed in Additional file 1: Figure S18. Figure 8 displays the estimates of sensitivity for each algorithm pair.

The ranking of algorithms was generally consistent regardless of which algorithm was chosen to determine calls in the verification set. DESeq2 had comparable sensitivity to edgeR and voom though less than DSS. The median sensitivity estimates were typically between 0.2 and 0.4 for all algorithms. That all algorithms had relatively low median sensitivity can be explained by the small sample size of the evaluation set and the fact that increasing the sample size in the verification set increases power. It was expected that the permutation-based SAMseq method would rarely produce adjusted P value <0.1 in the evaluation set, because the three vs three comparison does not enable enough permutations.

Precision Another important consideration from the perspective of an investigator is the precision, or fraction of true positives in the set of genes which pass the adjusted P value threshold. This can also be reported as 1−FDR. Again, ‘true’ differential expression was defined by an adjusted P value <0.1 in the larger verification set. The estimates of precision are displayed in Figure 9, where we can see that DESeq2 often had the second highest median precision, behind DESeq (old). We can also see that algorithms with higher median sensitivity, e.g., DSS, were generally associated here with lower median precision. The rankings differed significantly when Cuffdiff 2 was used to determine the verification set calls. This is likely due to the additional steps Cuffdiff 2 performed to deconvolve changes in isoform-level abundance from gene-level abundance, which apparently came at the cost of lower precision when compared against its own verification set calls.

To compare the sensitivity and precision results further, we calculated the precision of algorithms along a grid of nominal adjusted P values (Additional file 1: Figure S19). We then found the nominal adjusted P value for each algorithm, which resulted in a median actual precision of 0.9 (FDR = 0.1). Having thus calibrated each algorithm to a target FDR, we evaluated the sensitivity of calling, as shown in Additional file 1: Figure S20. As expected, here the algorithms performed more similarly to each other. This analysis revealed that, for a given target precision, DESeq2 often was among the top algorithms by median sensitivity, though the variability across random replicates was larger than the differences between algorithms.

The absolute number of calls for the evaluation and verification sets can be seen in Additional file 1: Figures S21 and S22, which mostly matched the order seen in the sensitivity plot of Figure 8. Additional file 1: Figures S23 and S24 provide heat maps and clustering based on the Jaccard index of calls for one replicate of the evaluation and verification sets, indicating a large overlap of calls across the different algorithms.

In summary, the benchmarking tests showed that DESeq2 effectively controlled type-I errors, maintaining a median false positive rate just below the chosen critical value in a mock comparison of groups of samples randomly chosen from a larger pool. For both simulation and analysis of real data, DESeq2 often achieved the highest sensitivity of those algorithms that controlled the FDR.

Model and normalization

For notational simplicity, the equations here use the natural logarithm as the link function, though the DESeq2 software reports estimated model coefficients and their estimated standard errors on the log2 scale.

Alternatively, the user can supply normalization constants s _ij calculated using other methods (e.g., using cqn [13] or EDASeq [14]), which may differ from gene to gene.

Expanded design matrices

For consistency with our software’s documentation, in the following text we will use the terminology of the R statistical language. In linear modeling, a categorical variable or factor can take on two or more values or levels. In standard design matrices, one of the values is chosen as a reference value or base level and absorbed into the intercept. In standard GLMs, the choice of base level does not influence the values of contrasts (LFCs). This, however, is no longer the case in our approach using ridge-regression-like shrinkage on the coefficients (described below), when factors with more than two levels are present in the design matrix, because the base level will not undergo shrinkage while the other levels do.

To recover the desirable symmetry between all levels, DESeq2 uses expanded design matrices, which include an indicator variable for each level of each factor, in addition to an intercept column (i.e., none of the levels is absorbed into the intercept). While such a design matrix no longer has full rank, a unique solution exists because the zero-centered prior distribution (see below) provides regularization. For dispersion estimation and for estimating the width of the LFC prior, standard design matrices are used.

Contrasts

where $\overrightarrow{c}$ represents a numeric contrast, e.g., 1 and −1 specifying the numerator and denominator of a simple two-level contrast, and ${\Sigma }_i=\text{Cov}\left({\overrightarrow{\beta }}_i\right)$, defined below.

Estimation of dispersions

We get final dispersion estimates from this model in three steps, which implement a computationally fast approximation to a full empirical Bayes treatment. We first use the count data for each gene separately to get preliminary gene-wise dispersion estimates ${\alpha }_i^{\text{gw}}$ by maximum-likelihood estimation. Then, we fit the dispersion trend α _tr. Finally, we combine the likelihood with the trended prior to get maximum a posteriori (MAP) values as final dispersion estimates. Details for the three steps follow.

The optimization in Equation (7) is performed on the scale of logα using a backtracking line search with accepted proposals that satisfy Armijo conditions [50].

Dispersion trend A parametric curve of the form (6) is fit by regressing the gene-wise dispersion estimates ${\alpha }_i^{\text{gw}}$ onto the means of the normalized counts, ${\bar{\mu }}_i$. The sampling distribution of the gene-wise dispersion estimate around the true value α _i can be highly skewed, and therefore we do not use ordinary least-squares regression but rather gamma-family GLM regression. Furthermore, dispersion outliers could skew the fit and hence a scheme to exclude such outliers is used.

The hyperparameters a ₁ and α ₀ of (6) are obtained by iteratively fitting a gamma-family GLM. At each iteration, genes with a ratio of dispersion to fitted value outside the range [10⁻⁴,15] are left out until the sum of squared LFCs of the new coefficients over the old coefficients is less than 10⁻⁶ (same approach as in DEXSeq [30]).

The parametrization (6) is based on reports by us and others of decreasing dependence of dispersion on the mean in many datasets [3]-[6],[51]. Some caution is warranted to disentangle true underlying dependence from effects of estimation bias that can create a perceived dependence of the dispersion on the mean. Consider a negative binomial distributed random variable with expectation μ and dispersion α. Its variance v=μ+α μ ² has two components, v=v _P+v _D, the Poisson component v _P=μ independent of α, and the overdispersion component v _D=α μ ². When μ is small, μ≲1/α (vertical lines in Additional file 1: Figure S1), the Poisson component dominates, in the sense that $v_{\text{P}}/v_{\text{D}}=1/\left(\mathrm{\alpha \mu }\right)\gtrsim 1$, and the observed data provide little information on the value of α. Therefore the sampling variance of an estimator for α will be large when μ≲1/α, which leads to the appearance of bias. For simplicity, we have stated the above argument without regard to the influence of the size factors, s _j , on the value of μ. This is permissible because, by construction, the geometric mean of our size factors is close to 1, and hence, the mean across samples of the unnormalized read counts, $\frac{1}{m}\sum _j{K}_{\mathit{\text{ij}}}$, and the mean of the normalized read counts, $\frac{1}{m}\sum _j{K}_{\mathit{\text{ij}}}/s_j$, will be roughly the same.

This phenomenon may give rise to an apparent dependence of α on μ. It is possible that the shape of the dispersion-mean fit for the Bottomly data (Figure 1A) can be explained in that manner: the asymptotic dispersion is α ₀≈0.01, and the non-zero slope of the mean-dispersion plot is limited to the range of mean counts up to around 100, the reciprocal of α ₀. However, overestimation of α in that low-count range has little effect on inference, as in that range the variance v is anyway dominated by the α-independent Poisson component v _P. The situation is different for the Pickrell data: here, a dependence of dispersion on mean was observed for counts clearly above the reciprocal of the asymptotic dispersion α ₀ (Figure 1B), and hence is not due merely to estimation bias. Simulations (shown in Additional file 1: Figure S25) confirmed that the observed joint distribution of estimated dispersions and means is not compatible with a single, constant dispersion. Therefore, the parametrization (6) is a flexible and mildly conservative modeling choice: it is able to pick up dispersion-mean dependence if it is present, while it can lead to a minor loss of power in the low-count range due to a tendency to overestimate dispersion there.

Therefore, ${\sigma }_{\text{lde}}^2\approx {\psi }_1\left(\right(m-p)/2)$, i.e., the sampling variance of the logarithm of a variance or dispersion estimator is approximately constant across genes and depends only on the degrees of freedom of the model.

Additional file 1: Table S2 compares this approximation for the variance of logarithmic dispersion estimates with the variance of logarithmic Cox–Reid adjusted dispersion estimates for simulated negative binomial data, over a combination of different sample sizes, number of parameters and dispersion values used to create the simulated data. The approximation is close to the sample variance for various typical values of m, p and α.

The prior variance ${\sigma }_{\text{d}}^2$ is thresholded at a minimal value of 0.25 so that the dispersion estimates are not shrunk entirely to ${\alpha }_{\text{tr}}\left({\bar{\mu }}_i\right)$ if the variance of the logarithmic residuals is less than the expected sampling variance.

where mad stands for the median absolute deviation, divided as usual by the scaling factor Φ ⁻¹(3/4).

Three or less residuals degrees of freedom When there are three or less residual degrees of freedom (number of samples minus number of parameters to estimate), the estimation of the prior variance ${\sigma }_{\text{d}}^2$ using the observed variance of logarithmic residuals $s_{\text{lr}}^2$ tends to underestimate ${\sigma }_{\text{d}}^2$. In this case, we instead estimate the prior variance through simulation. We match the distribution of logarithmic residuals to a density of simulated logarithmic residuals. These are the logarithm of ${\chi }_{m-p}^2$-distributed random variables added to $N(0,{\sigma }_{\text{d}}^2)$ random variables to account for the spread due to the prior. The simulated distribution is shifted by − log(m−p) to account for the scaling of the χ ² distribution. We repeat the simulation over a grid of values for ${\sigma }_{\text{d}}^2$, and select the value that minimizes the Kullback–Leibler divergence from the observed density of logarithmic residuals to the simulated density.

is, up to an additive constant, the logarithm of the density of prior (5). Again, a backtracking line search is used to perform the optimization.

For such genes, the gene-wise estimate ${\alpha }_i^{\text{gw}}$ is not shrunk toward the trended prior mean. Instead of the MAP value ${\alpha }_i^{\text{MAP}}$, we use the gene-wise estimate ${\alpha }_i^{\text{gw}}$ as a final dispersion value in the subsequent steps. In addition, the iterative fitting procedure for the parametric dispersion trend described above avoids that such dispersion outliers influence the prior mean.

Shrinkage estimation of logarithmic fold changes

As was observed with differential expression analysis using microarrays, genes with low intensity values tend to suffer from a small signal-to-noise ratio. Alternative estimators can be found that are more stable than the standard calculation of fold change as the ratio of average observed values for each condition [53]-[55]. DESeq2’s approach can be seen as an extension of these approaches for stable estimation of gene-expression fold changes to count data.

Empirical prior estimate To obtain values for the empirical prior widths σ _r for the model coefficients, we again approximate a full empirical Bayes approach, as with the estimation of dispersion prior, though here we do not subtract the expected sampling variance from the observed variance of maximum likelihood estimates. The estimate of the LFC prior width is calculated as follows. We use the standard iteratively reweighted least-squares algorithm [12] for each gene’s model, Equations (1) and (2), to get MLEs for the coefficients ${\beta }_{\mathit{\text{ir}}}^{\text{MLE}}$. We then fit, for each column r of the design matrix (except for the intercept), a zero-centered normal distribution to the empirical distribution of MLE fold change estimates ${\overrightarrow{\beta }}_r^{\text{MLE}}$.

To ensure that the prior width σ _r will be independent of the choice of base level, the estimates from the quantile matching procedure are averaged for each factor over all possible contrasts of factor levels. When determining the empirical upper quantile, extreme LFC values ($\left|{\beta }_{\mathit{\text{ir}}}^{\text{MLE}}\right|>log\left(2\right)10$, or 10 on the base 2 scale) are excluded.

and α _i is the final dispersion estimate for gene i, i.e., ${\alpha }_i={\alpha }_i^{\text{MAP}}$, except for dispersion outliers, where ${\alpha }_i={\alpha }_i^{\text{gw}}$.

where the current fitted values ${\mu }_j=s_j{e}^{\sum _r{x}_{\mathit{\text{jr}}}{\beta }_r}$ are computed from the current estimates $\overrightarrow{\beta }$ in each iteration.

where $\ell \left({\overrightarrow{\beta }}_i;\overrightarrow{K_i},{\alpha }_i\right)$ is the logarithm of the likelihood, and partial derivatives are taken with respect to LFC β _ir . For a negative binomial GLM, the observed Fisher information, or peakedness of the logarithm of the profile likelihood, is influenced by a number of factors including the degrees of freedom, the estimated mean counts μ _ij , and the gene’s dispersion estimate α _i . The prior influences the MAP estimate when the density of the likelihood and the prior are multiplied to calculate the posterior. Genes with low estimated mean values μ _ij or high dispersion estimates α _i have flatter profile likelihoods, as do datasets with few residual degrees of freedom, and therefore in these cases the zero-centered prior pulls the MAP estimate from a high-uncertainty MLE closer toward zero.

Wald test

The tail integrals of the standard normal distribution are multiplied by 2 to achieve a two-tailed test. The Wald test P values from the subset of genes that pass the independent filtering step are adjusted for multiple testing using the procedure of Benjamini and Hochberg [21].

Independent filtering

Independent filtering does not compromise type-I error control as long as the distribution of the test statistic is marginally independent of the filter statistic under the null hypothesis [22], and we argue in the following that this is the case in our application. The filter statistic in DESeq2 is the mean of normalized counts for a gene, while the test statistic is p, the P value from the Wald test. We first consider the case where the size factors are equal and where the gene-wise dispersion estimates are used for each gene, i.e. without dispersion shrinkage. The distribution family for the negative binomial is parameterized by θ=(μ,α). Aside from discreteness of p due to low counts, for a given μ, the distribution of p is Uniform(0,1) under the null hypothesis, so p is an ancillary statistic. The sample mean of counts for gene i, ${\bar{K}}_i$, is boundedly complete sufficient for μ. Then from Basu’s theorem, ${\bar{K}}_i$ and p are independent.

While for very low counts, one can observe discreteness and non-uniformity of p under the null hypothesis, DESeq2 does not use the distribution of p in its estimation procedure – for example, DESeq2 does not estimate the proportion of null genes using the distribution of p – so this kind of dependence of p on μ does not lead to increased type-I error.

If the size factors are not equal across samples, but not correlated with condition, conditioning on the mean of normalized counts should also provide uniformly distributed p as with conditioning on the mean of counts, ${\bar{K}}_i$. We may consider a pathological case where the size factors are perfectly confounded with condition, in which case, even under the null hypothesis, genes with low mean count would have non-uniform distribution of p, as one condition could have positive counts and the other condition often zero counts. This could lead to non-uniformity of p under the null hypothesis; however, such a pathological case would pose problems for many statistical tests of differences in mean.

We used simulation to demonstrate that the independence of the null distribution of the test statistic from the filter statistic still holds for dispersion shrinkage. Additional file 1: Figure S26 displays marginal null distributions of p across the range of mean normalized counts. Despite spikes in the distribution for the genes with the lowest mean counts due to discreteness of the data, these densities were nearly uniform across the range of average expression strength.

Composite null hypotheses

DESeq2 offers tests for composite null hypotheses of the form ${\mathcal{\mathscr{H}}}_0:\left|{\beta }_{\mathit{\text{ir}}}\right|\le \theta$ to find genes whose LFC significantly exceeds a threshold θ>0. The composite null hypothesis is replaced by two simple null hypotheses: ${\mathcal{\mathscr{H}}}_{0a}:{\beta }_{\mathit{\text{ir}}}=\theta$ and ${\mathcal{\mathscr{H}}}_{0b}:{\beta }_{\mathit{\text{ir}}}=-\theta$. Two-tailed P values are generated by integrating a normal distribution centered on θ with standard deviation SE(β _ir ) from |β _ir | toward ∞. The value of the integral is then multiplied by 2 and thresholded at 1. This procedure controls type-I error even when β _ir =±θ, and is equivalent to the standard DESeq2 P value when θ=0.

Conversely, when searching for genes whose absolute LFC is significantly below a threshold, i.e., when testing the null hypothesis ${\mathcal{\mathscr{H}}}_0:\left|{\beta }_{\mathit{\text{ir}}}\right|\ge \theta$, the P value is constructed as the maximum of two one-sided tests of the simple null hypotheses: ${\mathcal{\mathscr{H}}}_{0a}:{\beta }_{\mathit{\text{ir}}}=\theta$ and ${\mathcal{\mathscr{H}}}_{0b}:{\beta }_{\mathit{\text{ir}}}=-\theta$. The one-sided P values are generated by integrating a normal distribution centered on θ with standard deviation SE(β _ir ) from β _ir toward −∞, and integrating a normal distribution centered on −θ with standard deviation SE(β _ir ) from β _ir toward ∞.

Note that while a zero-centered prior on LFCs is consistent with testing the null hypothesis of small LFCs, it should not be used when testing the null hypothesis of large LFCs, because the prior would then favor the alternative hypothesis. DESeq2 requires that no prior has been used when testing the null hypothesis of large LFCs, so that the data alone must provide evidence against the null hypothesis.

Interactions

Two exceptions to the default DESeq2 LFC estimation steps are used for experimental designs with interaction terms. First, when any interaction terms are included in the design, the LFC prior width for main effect terms is not estimated from the data, but set to a wide value (${\sigma }_r^2={(log(2\left)\right)}^{2}1000$, or 1000 on the base 2 scale). This ensures that shrinkage of main effect terms will not result in false positive calls of significance for interactions. Second, when interaction terms are included and all factors have two levels, then standard design matrices are used rather than expanded model matrices, such that only a single term is used to test the null hypothesis that a combination of two effects is merely additive in the logarithmic scale.

Regularized logarithm

where β _ij is the shrunken LFC on the base 2 scale for the jth sample. The variance of the prior is set using a similar approach as taken with differential expression, by matching a zero-centered normal distribution to observed LFCs. First a matrix of LFCs is calculated by taking the logarithm (base 2) of the normalized counts plus a pseudocount of $\frac{1}{2}$ for each sample divided by the mean of normalized counts plus a pseudocount of $\frac{1}{2}$. The pseudocount of $\frac{1}{2}$ allows for calculation of the logarithmic ratio for all genes, and has little effect on the estimate of the variance of the prior or the final rlog transformation. This matrix of LFCs then represents the common-scale logarithmic ratio of each sample to the fitted value using only an intercept. The prior variance is found by matching the 97.5% quantile of a zero-centered normal distribution to the 95% quantile of the absolute values in the LFC matrix.

Cook’s distance for outlier detection

R/Bioconductor package

DESeq2 is implemented as a package for the R statistical environment and is available [10] as part of the Bioconductor project [11]. The count matrix and metadata, including the gene model and sample information, are stored in an S4 class derived from the SummarizedExperiment class of the GenomicRanges package [60]. SummarizedExperiment objects containing count matrices can be easily generated using the summarizeOverlaps function of the GenomicAlignments package [61]. This workflow automatically stores the gene model as metadata and additionally other information such as the genome and gene annotation versions. Other methods to obtain count matrices include the htseq-count script [62] and the Bioconductor packages easyRNASeq [63] and featureCount [64].

The DESeq2 package comes with a detailed vignette, which works through a number of example differential expression analyses on real datasets, and the use of the rlog transformation for quality assessment and visualization. A single function, called DESeq, is used to run the default analysis, while lower-level functions are also available for advanced users.

Read alignment for the Bottomly et al. and Pickrell et al.datasets

Reads were aligned using the TopHat2 aligner [65], and assigned to genes using the summarizeOverlaps function of the GenomicRanges package [60]. The sequence read archive fastq files of the Pickrell et al. [17] dataset (accession number [SRA:SRP001540]) were aligned to the Homo sapiens reference sequence GRCh37 downloaded in March 2013 from Illumina iGenomes. Reads were counted in the genes defined by the Ensembl GTF file, release 70, contained in the Illumina iGenome. The sequence read archive fastq files of the Bottomly et al. [16] dataset (accession number [SRA:SRP004777]) were aligned to the Mus musculus reference sequence NCBIM37 downloaded in March 2013 from Illumina iGenomes. Reads were counted in the genes defined by the Ensembl GTF file, release 66, contained in the Illumina iGenome.

Reproducible code

Sweave vignettes for reproducing all figures and tables in this paper, including data objects for the experiments mentioned, and code for aligning reads and for benchmarking, can be found in a package DESeq2paper [66].