April 11, 2015

Differential *omics in theory and in practice

This is a comment for a required course. The initial paper of interest is Dudoit’s paper Statistical methods for identifying differentially expressed genes in replicated cDNA microarray experiments. Though the paper itself is over a decade old, it provides a necessary introduction to oligonucleotide array technology and some of the errors associated with it. Due to the awesomeness of inkjet printing, custom oligo arrays can be built for any kind of DNA reporter, but they can further be used for combinatorial mutagenesis. In the intervening years, RNA-seq has become the tool of choice for investigating gene expression data; and while the principles outlined in Dudoit 2002 have remained the same, the theory and practice of differential *omics are much evolved. Note that differential expression is but one of many A/B testing experiments that follow the same pattern; others include differential methylation (bisulfite sequencing), differential histone modification (ChIP-seq), differential chromatin state (ATAC-seq), and so on and so forth. Quite honestly, old-fashioned GWAS falls into this category too. While each specific application of A/B testing has its own particular concerns, these concerns fall into categories with near-perfect overlap.

Part 1: Units

Chips yield intensity values, sequencing yields read counts. That’s about it, right? Well, think about DNA-based studies (SNP/Indel/CNV) for a moment. These studies don’t “operate” on the level of intensity (chip) or read counts (seq), they operate on the level of the genotype. Hom-ref, hom-var, or het. The unit we want to test here is the allele. There’s an entire layer of inference between the measured units (intensity or read counts) and the allele: things like Birdseed or zCall will infer allelic state from raw oligo intensities; while programs like the GATK Haplotype Caller or Freebayes will perform this inference from aligned reads.

But genotypes turn out to be the only place you can really do this. In theory, methylation should follow the same process, but since typically cell populations (not single cells) are sequenced, there are very many CpG sites which are intermediately-methylated; this makes it more similar to pooled DNA sequencing experiments than it is to standard exome/genome-seq. The unit becomes the methylation frequency; and similar maximum-likelihood approaches such as MLML can be used to estimate these. For methylation arrays (such as the Illumina Infinium HM450 chip), this estimation is not performed; instead the raw log(R/G) values are used after suitable data normalization (see Part 2).This is a general trend for chip data.

What’s the ideal unit for mRNA? I think it should be the concentration of each mRNA in solution. That is, the ideal unit is mol/L. Note that this is an absolute measure: as stoichiometry is in general nonlinear, there are regimes where the same relative concentration ([transcript mRNA]/[all mRNA]) may result in vastly different translational dynamics, particularly in the presence of translational regulators such as FMRP. The estimation of absolute concentration from RNA-seq does not appear to have been attempted; and typically library preparation itself should alter absolute concentrations in a nontrivial way. So maybe we should forget about absolute concentration, and focus instead on relative mRNA concentration. One way to estimate this might be via

\frac{[\mathrm{tx}]}{[\mathrm{all}]} \approx \frac{\mathrm{reads\;in\;gene}}{\mathrm{gene\;length} \times \mathrm{total\;reads}} = \frac{r_g}{\ell_g \times R} = \hat{[g]}_R

This approximation makes the assumption that R \propto \mathrm{total\; transcripts}, and is a well-known quantity. Indeed, the quantity above is

\hat{[g]}_R = 10^9\times \mathrm{RPKM}_g

where RPKM is the well known Reads per Kilobase per Million Reads. However, Wagner, Kin, and Lynch point out that there are better estimates for the total abundance of transcripts, and introduce a related measure, TPM, in place of RPKM.

This all goes out the window with array data. Instead of counts, one has two-channel intensities for competitively-bound cDNA, and these intensities are some (hopefully monotonic) function of post-library-construction absolute concentration. While you’d like to have a measure of relative concentration (relative to the total mRNA concentration), you’re stuck with relative intensity (relative to whatever reference mRNA sample you used) per gene. While there is literature in fitting Langmuir or stoichiometric models to titration experiments, which enables a direct estimate of absolute mRNA concentration from probe intensity, these models cannot be directly applied to expression microarrays. First, the models in these papers were fit to different arrays; second, in order to train the parameters, tens of thousands of titration experiments would need to be performed to fit calibration curves for each appropriate (mRNA, probe) pair; and, even should these be fit to a single chip, synthesis efficiency during manufacturing is poor enough that the resulting estimates would be very noisy.

But even stuck with relative intensities, there’s still a question about the correct axes. Dudoit 2002 makes a great deal about the (M, A) = (log R/G, log R*G) versus (logR, logG) axes, even though these coordinate systems are linearly related. From a pure dimensional analysis perspective, log R/G is most appealing, as the quantity R/G is dimensionless, and so the log doesn’t screw up any units.

For splicing, again, ideally we would want isoform-level absolute concentrations. We could settle for isoform-level relative concentrations (TPM as for expression), but breaking down total mRNA abundance for a gene (viewed as the union of all of its isoforms) into abundance for each isoform separately turns out to be a fairly difficult inference problem. Instead, differential splicing (and spliceQTLs) tend to focus on the exon inclusion fraction, \psi_i: the proportion of mRNA, for a given gene, which contain the ith exon. There are many, many models for estimating \psi. DEXSeq uses a generalized linear model (negative binomial), the mean parameter of which is \psi, SpliceTrap takes a Bayesian approach (combinations of normals and betas) to estimate \psi, MATS uses a similar approach but with the binomial as opposed to normal distribution, and Xiong et al use a beta-binomial model with a positional bootstrap to account for mapping biases (see SM of that paper).

How about for differential histone modification? The important biological detail here is, for a given locus, what proportion of chromosomes have a histone with the given modification sitting at that locus. For non-histone ChIP-seq, such as for transcription factor binding, the story becomes more complicated, as the protein may directly bind DNA, or indirectly bind (i.e. as a part of a complex where some other TF binds). Here, the unit is the affinity-frequency distribution; that is, the frequency of direct and indirect binding, where “degree of directness” is itself a real-valued parameter to be inferred from the data. ChIPDiff uses a beta-binomial model to perform an initial, local estimate of chromatin modification frequency within groups (p_A and p_B). It combines this with an HMM to aggregate information over multiple small bins, to estimate the indicator function

I[p_A/p_B > \tau] and I[p_B/p_A > \tau].

Many other methods (F-Seq, dCaP, and Wu’s Nonparametric) utilize the naive estimator

\langle \mathrm{bin} \rangle = \frac{r_{\mathrm{bin}}}{\ell_{\mathrm{bin}}\cdot R}

not as an estimate of p_i, but rather as one piece of the final test statistic (for instance \langle \mathrm{bin} \rangle_A - \langle \mathrm{bin} \rangle_B).

Part 2: Normalization

Surely, having as best as possible placed your data in the appropriate units, you are ready to proceed to differential expression! FPKM is all the normalization I need! Let’s say you’ve done basic high-throughput exome sequencing on two flowcells of HiSeq, genotyped each separately, and have some 50-100 samples’ worth of data. You take your genotypes, and perform PCA. Much to your chagrin, one of the top PCs is the flowcell. You go online (say to seqanswers) and they suggest that you put the raw reads together and jointly genotype all the samples — and maybe add some 1000 Genomes samples for good measure. You do so, repeat the PCA, and find that none of the top PCs correlate with flowcell. You may not think this is normalization, but it really is. In particular you normalized out coverage and artefactual variation that are due to differences in library preparation and Illumina’s manufacturing process. These artifacts, whether due to small variations in reagent concentration, temperature, cycling time, the accuracy of manufacturing, the initial quantity of your sample, the generation number of cell lines, (&c &c &c) distort your measurements. They’re noise. Some effects are subtle, and can be controlled for as covariates (see part 3); others are the dominant source of variance, and somehow they need to be removed before you can even start. For oligonucleotide arrays, the major distortion is due to manufacturing differences; for *seq efforts, it’s total read depth. Removing these particular effects is referred to as normalization.

logR/G-logRG (M-A) plot of zebrafish expression microarray, with loess curves for each print head. Obtained from http://lectures.molgen.mpg.de/Microarray_WS0304/anja_VL_25_11_2003.ppt

logR/G-logRG (M-A) plot of zebrafish expression microarray, with loess curves for each print head.
Obtained from here.

Dudoit 2002 references nonparametric regression (Loess) as a means of correcting for printhead-specific biases. This is still the standard approach for analyzing (or re-analyzing) microarray data — and the Loess is performed within printhead and within sample; this enables one to compare across multiple chips. An example is shown above, where the multiple lines show how different print heads lead to different smoothed M-A curves. The goal would be to shift each of these curves to some “reference” curve. One advantage of Loess is that the smoothing model can be semiparametric and include other kinds of error covariates (such as sequence GC%, gene length, and so on). Another approach introduced in Bolstad 2003 is quantile normalization. It should really be called “rank normalization”. Consider having performed four RNA-seq experiments and calculated RPKMs (or equivalent) for these samples. Something typical to see looks like: quantile_ex Here there are slight distortions making the cumulative (rank) distributions not equal. Something very common is zero-inflation: distortion about genes with zero or very few reads.This can be due to inefficient ribosomal RNA depletion — ribosomal RNA so dominates that even a small variance can render RPKM calculations not directly comparable across experiments.

Quantile normalization (“rank normalization”), in it’s most aggressive form, replaces each curve in the above plot by the average curve. Suppose, for instance, that in sample i, gene j is the 5000th gene (when sorted by RPKM). Then the expression value g_{ij} is replaced by the average expression of the 5000th gene across all samples. Note that which gene is gene 5000 will differ between samples. That is, we directly force the cumulative distributions of all samples to match, while constraining the transformation to be rank-preserving within each sample, so that there is no variance within ranks, but there is still variance within genes. While this approach was developed particularly for competitive hybridization (where the R and G channels would be separately transformed, thereby indirectly normalizing the M and A plots), it is also regularly applied to RNA-seq — particularly in data sets with widely varying library complexities or RNA integrity numbers.

This degree of tampering is entirely unphysical; so there are less heavy-handed approaches which, rather than forcing every rank to match exactly, choose a set of “plausibly invariant” measurements (things whose expression should match — e.g. housekeeping genes or spike-ins), and fit a smooth function f(rank, expr) = expr_{\mathrm{new}} which forces (as much as possible) the expression of the invariant genes to match. A very nice explication of these approaches can be found here.

Quantile normalization has been extended to regress away technical covariates as well, resulting in conditional quantile normalization, which regresses out covariates using cubic splines, and then applies quantile normalization to the residuals to attempt to match a target distribution; this normalization is directly applied to highly-expressed genes, and extended (via an approximation) to genes with lower expression. In practice, full quantile normalization does not appear to add additional power to detect differentially-expressed genes over simply dividing the entire expression distribution by a single summary such as the 1st quartile (Bullard, 2010). Nevertheless, for some work I have done in the past, we felt the warping of gene expression distributions between samples was mainly due to experimental artifacts, and so full rank normalized (with CQN) to a carefully-constructed and replicated reference distribution (similar to the use of Brain atlases in MRIs).

The ERCC proposed a set of RNA spike-in standards to aid in normalization (the idea is the absolute concentration of these unique RNA sequences is known up-front, and can be used to calibrate across experiments). However, the resulting reads are still too unstable to be sufficient for normalization purposes – I remember hearing frustration about this from a number of labs.

Empirically, DESeq’s approach (each gene is separately normalized by the geometric mean) appears to perform the best, but not much better than other approaches. Notably, this paper does not include CQN in the comparison. The modern standards are dChip and IRON.

The current standard in microarray expression analysis presents an odd paradox: while for a given experiment, the Loess or full quantile normalization methods are used; normalizing across experiments (for instance, analyzing multiple published microarray datasets) utilizes an array of novel methods not typically applied within a single experiment. This seems a bit strange, as cross-batch normalization should reduce to within-batch normalization if the number of batches is 1 (and let’s completely ignore the issue of what constitutes a “batch”). Lazar et al. make a distinction between three sources of error: expression heterogeneity, batch effects, and other sources of error. The origination of batch effects, they claim, is the simple fact that only a fixed set (typically 96) of samples can be processed together. In fact, the “batch” unit is just a proxy for a number of other sources of variation: library prep, experimental conditions at time of processing, and so forth. In general, within a batch there is not necessarily a good proxy for these sources of intensity (or expression) variation, but across multiple batches they can be controlled, by using the batch as a proxy. While nonparametrics like the above (LOESS or CQN against a reference distribution) still apply in this case, they are typically not used. Instead, parametric batch normalization typically recenter and rescale RPKM (or logR/G) values to have the same mean and variance across batches. While gene i and gene j may have different means, gene i in batch 1 is forced to have the same mean and variance as gene i in batch 2 (and so on and so forth). These normalizations can be performed in the linear or logarithmic scale. This basic approach can be extended to linear models which allow the incorporation of other covariates, but the idea is the same: estimate per-batch means and variances, and adjust the data so that these parameters are homogenous across batches for each gene. Other methods are unsupervised or latent in that they assume the primary sources of variation are nonbiological (we will see this again in statistical testing). Under this assumption, latent variables can be extracted from the expression matrix via PCA; and these are assumed to be technical sources (indeed, batch usually correlates highly with one of the top principal components). All of these methods are reviewed in Lazar et al. linked above.

The practical approach here is pretty straightforward: use the QQ-plot as a readout of how well experimental or batch differences have been controlled. A QQ-plot that is for the most part well-calibrated (we expect differential expression for a small fraction of genes only) indicates that normalization has worked effectively. Thus there’s a straightforward practical procedure: start with basic mean-variance normalization between batches, run your statistical test, and check calibration. If it’s not calibrated, pick a normalization method more or less at random and apply it; recalculate your statistics and check if the QQ-plot looks good. Lather. Rinse. Repeat.

I hope that doesn’t shatter any ideas about Very Serious Statisticians poring over a dataset and considering which model most applies to the situation, choosing appropriately based on visualization of the data and theoretical justifications, and nodding approvingly at the results. That’s not how it works for machine learning, and it’s really not how it should work for the practice of statistics. When you’ve got lots of null hypotheses, it’s really hard to argue with well-calibrated test statistics, just as it’s hard to argue with a high CVAUC. Theoretical considerations happen at the margins, but the main thing is: if you see a crappy QQ plot, you went off the rails somewhere, so it’s time to try something else.

Effectively the same approaches apply to ChIP-seq. Bailey, et al. quickly review several standard normalization procedures: depth normalization, linear normalization, reference-based normalization, LOESS, and quantile. See the paper for specific references. This can be extended to spike-ins or control samples, which is the approach taken by NCIS. At the same time, ChIP-seq (and Hi-C and clip-seq) provide additional challenges which are not entirely addressed by the above methods. These technologies have nonspecific backgrounds which are heavily dependent on DNA sequence and small variations in antibody concentration or binding efficiency during the experiment. While backgrounds are present in RNA-seq, it is generally a small enough proportion that it can be ignored. By contrast, since ChIP methods tend to rely on peak-calling (identifying bound regions by virtue of normalized/smoothed read depth exceeding a threshold), the variation of the background signal needs to be accounted for. Consider for instance two technical replicates with the same number of aligned reads; the replicate with a higher background will, because of the constraint of having the same total reads, have smaller peaks on average. A normalization approach to deal with this (as opposed to direct statistical modeling, see below) is to combine background subtraction with one of the above methods. That is, all read depths are adjusted by subtracting the background estimate (either a constant, or the result of a fitted model that maps genomic features to expected reads due to background). The resulting counts can then be normalized to a reference distribution following any of the methods described above.

More sophisticated methods do not treat the background during data normalization, but instead model it directly during statistical testing. This is the approach taken by dCaP and ChIPComp. It’s worth asking: in all these cases, seeing as the transformations are generally rank-preserving within sample, why perform normalization at all? Statistics could be calculated on the ranks within samples as opposed to on the direct expression/intensity/frequency estimates. The reason for this is that using ranks results in a p-value without a biologically-related effect estimate, and estimates of fold increase/decrease are important not only for interpretation, but for understanding results in context. Normalization considerations are more about retaining effect size than they are about finding some way of getting a calibrated p value.

Part 3: Testing for differences (or: the triumph of the LMM)

Dudoit 2002 uses a simple T statistic for testing differential expression. How have we progressed in the past decade? We’re still using (pretty much) a T statistic, although in an asymptotic guise from the LMM (or GLMM). Where we have gotten much better are in providing proxies for error covariates, and in modeling the distributions of read counts or genotyping errors. I have written about specific cases before. The general conclusion is that likelihood-based regressions result in powerful tests with well-controlled false-discovery rates. The use of a linear mixed model can even obviate the need for location-scale normalization: by including mean and variance components, batch effects can be adjusted during model fitting, without need for a separate normalization step.

Differential binding from ChIP/Clip/Hi-C is the new kid on the block. Even so, there are lots of models for statistical prediction of differentially enriched regions. These have all been developed for ChIP, but almost immediately extend to other link-digest-sequence experiments. What’s surprising is the variety of models in this area. DIME uses a mixture model after Loess normalization. MAnorm fits a linear model and tests the residuals, jMOSAiCS uses a graphical model with nodes of the form

Z \sim \mathrm{NegBin}(a, a \mathrm{exp}[-(\beta_0 + \beta_1 X^c)])

PePr normalizes ChIP peaks within sample and performs an asymptotic (Wald) test after fitting a negative binomial distribution, after extensive preprocessing and normalization. dCaP uses a LMM with a normal approximation, while dPCA compares global patterns between two conditions by decomposing the difference between multiple ChIP signals. ChIPComp uses a hierarchical model of a Poisson sampling distribution atop a linear model, and demonstrate a well-calibrated null distribution.

By contrast, differential expression, splicing, methylation, variant association and QTL studies, are almost all linear mixed models of various flavors. Wockner, et al. use LIMMA for differential methylation analysis. However, even though methylation occurs at specific CpG loci, differential methylation is typically observed in regions; and many methods have been developed to associate not just individual loci, but to test entire regions for differential methylation, either by aggregation or direct testing. Robinson, et al. list 14, of which at least 8 heavily involve linear models. For splicing, ARH-seq uses an entropy-based method, while rMATS is a GLM (logit) model. In practice, the only way to appropriately include covariates is through some kind of linear model. For instance, a very standard expression model is:

\mathrm{log} \mathrm{TPM}_k = d_k + \mathrm{RIN}_k + \mathrm{case}_k + \sum_{i=1}^p s_{ik} + \sum_{i=1}^r b_{ik} + \sum_{i=1}^\ell c_{ik} + \epsilon_k

\vec \epsilon \sim N(0, \sigma_g^2\mathrm{G} + \sigma_e^2I)

Where d is the depth, RIN is the RNA integrity, case is case status (it may also be the tissue type indicator), the s are individual genotypes one may want to control for, the b are “latent factors” (typically the top r principal components of the expression matrix, assumed to be nonbiological factors), c are clinical covariates (such as age, gender, BMI, etc), and G is the genetic relationship matrix, ideally calculated excluding the cis-region of the gene of interest, and excluding variants related to case/control status. The statistical test here is typically one of: a Wald test on the case coefficient; a likelihood ratio test (case included vs case excluded); or a score test (fit everything else, test the covariance between the case indicator and the residuals — care should be taken when random effects are included in this setting).

For other methods (take ARH-seq, for instance), in order to adjust for covariates, the above model would need to be fit (without the case variable) and the effects of covariates removed. NOISeq is the above model, equipped with a fixed coefficient on d, without any other covariates, and using the empirical distribution to estimate \sigma_e^2 (or even replacing the normal with the empirical noise distribution). Soneson et al find that, empirically, LIMMA (a direct implementation of the above model) is quite robust, performing well in most situations; similarly Seyednasrollah et al find that for small sample sizes, LIMMA identifies the most number of genes at low FDR (high precision – see fig 2). The best part about the linear model here is: if you test the coefficients on s instead of “case”, you’ve just performed an eQTL analysis; and the models for eQTLs (ICE-EMMA, PANAMA, svaseq, Matrix eQTL, PEER, and HEFT) are all linear models, their only differences being implementation detail, and how certain covariates or latent factors are calculated.

This review is far from comprehensive, but I think it captures the practice of differential *omics as it is today. As we move forward, there’s going to be additional work particularly in crosslink-and-seq (ChIP/clip/Hi-C) and methylation statistics to better incorporate technical covariates into the detection of differentially modified or differentially bound regions. And, of course, there’s the big open question: how do we put it all together? (But that’s a topic for another post).

Update Aug 18 2015

The Pachter Lab has recently released announced Sleuth for testing differential expression. Professor Pachter makes an extremely good point about the necessity of estimating transcript-level abundances, and that these estimates induce technical variation due to read ambiguity. The solution is another LMM (well, what did you expect?), with boostrap-derived estimates of technical variance included in the variance component. I will be checking Kallisto/Sleuth (Доверяй, но проверяй), particularly on microRNA and mini-exons, and switch to using it in place of Bowtie+CL+Limma-VOOM. I would speculate that the Kallisto/Sleuth pipeline probably functions well (with some paramater tuning) on other feature quantifications (ChIP/Clip/Hi-C).


June 19, 2013

Genetic Association and the Sunrise Problem

Filed under: Uncategorized — Tags: , , , , — heavytailed @ 3:42 am

As a preface, let me acknowledge that this blog has been perhaps a bit too preoccupied with statistical genetics in the past month. Looking at the several posts I have partially completed it is likely to remain so through the summer.

Sequencing and GWAS

Nature Genetics has in the past few months returned to its old position as a clearinghouse for GWAS studies, the author lists for which steadily increase as more and more groups contribute data. (Can we start putting the author list in the supplemental material? It’s getting hard to navigate the webpage…). GWAS studies are nice, we sort of know how to do them. I have a bit of a beef with the push-button approach, I think GWAS studies and in particular meta/mega analyses are failing to deliver as much information as they should, and I’ll come back to this at the end of the section. But GWAS always have the complexity that they are ascertained. We didn’t find a variant of effect T. Does one exist? Can’t say, we could only query these X variants.

Sequencing is fundamentally different: whatever effects are driving the phenotype in your sample are present in your sample. Yet the treatment of (particularly exome) sequencing studies is “like a GWAS just with more variants,” with no real use of the fact that variants are discovered rather than ascertained. It’s the same kind of “where is the signal I can find?” question. But really, the trait is heritable, the signal is there, somewhere, and it’s not just about the signals you can find, it’s also about the places you can rule out. This applies to GWAS as well: you genotyped 50,000 samples and have 12 hits. Surely you can say something else about the other 199,988 sites on the chip, right? Or at least about a large fraction of them?

And once you go from ascertainment to discovery, you can rule out whole portions of the variant space. Things like “No variant in SLC28A1 of frequency > 5% has an odds ratio >1.2”. With that said do I still care about SLC28A1 as a candidate gene for my trait? What if the best I can do for ADAM28 is to say no such variant exits with OR>2.6, but may exist for OR<2.6? Now how much do I care about SLC28A1? You can make such statements having performed sequencing, not only can you produce a list of things where signal definitely is, but you can segment the rest into a list of things where the signal definitely is not, and those where signal might be.

In some sense GWAS studies dropped the ball here too, but the analysis is far more subtle. One of the big uses of modern sequencing data is fine mapping: so, at a GWAS locus, trying to identify rare variants that might be generating a “synthetic association”. For instance, if several rare variants of large effect happen to be partially tagged by the GWAS hit. However, given the observed variance explained, there’s then a posterior estimate of frequency, effect, r^2, and number of variants that could be consistent with the observed signal. Carefully working out what could be there, and what’s expected to be there would provide not only intuition about what to expect when performing fine mapping, but a good and precise framework for thinking about synthetic associations. While the idea that most GWAS loci are so explained has been vigorously rebutted, it is done so at the level of bulk statistics, with little attention paid to if there is a synthetic association here, what must such variants look like?

The point is ultimately there’s a lot more information than what things have p<5e-7, it just needs to be extracted.

Bounding Variant Effects

The 0th-order question is “What variants do I have with p<5e-7“. If the answer isn’t the empty set, the 1st-order question is “What genes are near these variants?” and the 2nd-order question is “What biological processes are these genes involved in?”. If the answer is the empty set, the 1st-order question is “What gene burden tests are at the top of the quantile-quantile plot?”, the 2nd-order question is “What biological processes are these genes involved in?”

But, as I mentioned in the previous section, you’ve seen these variants enough times (especially now with tens- to hundreds of thousands of samples) to know whether or not they’re interesting. The first-order question ought to be “What variants can I rule out as contributing substantially to disease heritability [under an additive model]?” Ideally, this would be effectively everything you looked at. In practice, you looked at 100,000-10,000,000 variants, and some of those will look nominally associated by chance, and these will be difficult to rule out.

Alright so what am I talking about? Here’s the model:

\mathbb{P}[Y=1|X,C_1,C_2,\dots] = \alpha + \beta X + \sum_i \tau_i C_i + \epsilon

where X are the genotypes at a site, and C_i is the ith covariate. It is the property of maximum likelihood that, given the data, the coefficient vector (\alpha^*,\beta^*,\tau_1^*,\dots) = V ^*\sim N(V_{\mathrm{true}},-[\nabla^2\mathcal{L}|_{V_{\mathrm{true}}}]^{-1}). Denoting the variance-covariance matrix as \Sigma then \beta \sim (\beta_{\mathrm{true}},\Sigma_{22}). This posterior distribution on the estimate allows more than the basic test of \beta_{\mathrm{true}} = 0, one can also ask for what values (\beta_u,\beta_l) we have \mathbb{P}[\beta_{\mathrm{true}} > \beta_u | \beta^*] < p, \mathbb{P}[\beta_{\mathrm{true}} < \beta_l | \beta^*] < p. This is just a p-ile confidence interval, but if p<1e-6 and \beta_u-\beta_l is small with \beta_l < 0 < \beta_u, then this particular variant is very unlikely to be causal, given these bounds, in that the probability of a large beta is very low.

Now there are two problems with “just using a confidence interval.” First, because the likelihood is heavily dependent on the number of observations of nonzero X_i, the variance of the estimator is an increasing function of the minor allele frequency. That is, rare variants are harder to bound. Secondly, the disease heritability conferred by a variant of given effect increases with allele frequency. That is, a 1.4 odds ratio variant at 0.5% frequency is, in and of itself, contributing very little to the prevalence of the disease. By contrast, a 1.4 odds ratio variant at 30% frequency is contributing a large fraction of disease heritability.

Both problems can be resolved by taking a heritability view, that is, asking instead the question for what proportion \rho(\beta,f) of phenotypic variance we have

\mathbb{P}[\rho(\beta_{\mathrm{true}},f_{\mathrm{true}}) > T | \beta^*,f^*]

In other words, say you observe a variant with \beta = 0.2 \pm 0.25, at a frequency of 0.01. You then ask, what is the probability that this variant explains 1% of the total prevalence (on a liability scale) of my disease, given this observation? Well, that’s simple, given the prevalence and frequency, one can simply ask for which two values of beta, \beta_{\mathrm{R}},\beta_{\mathrm{P}}, the risk-effect and protective-effect values, is the proportion of phenotypic variance 1%. Then, given those values, use the posterior distribution to ask what is \mathbb{P}[\beta_{\mathrm{true}} > \beta_{\mathrm{R}} | \beta^*]?

Note that the frequency of the variant does not enter into the discussion, it’s only hidden in the calculations of the phenotypic variance \rho(\beta,f), and the standard deviation of the maximum likelihood statistic \beta^*, thus making variants of different frequencies commensurate by placing the hypotheses on the same scale – and one growing approximately with the variance of the estimator. That is, while the variance of the estimator increases as the variant becomes rare (this is what makes bounding using a constant odds ratio difficult), so too does the effect size required to confer a given level of phenotypic variance. These phenomena tend to cancel, so on the scale of variance explained, one can bound a rare variant as well as a common variant.

In order to do this, it’s just a question of converting a given variance explained into frequency-effect pairs, and evaluating the likelihood of such pairs given the data. That is:

= \mathbb{P}[\rho(\beta_{\mathrm{true}},f_{\mathrm{true}}) > T | \beta^*,f^*,f_{\mathrm{true}}]\mathbb{P}[f_{\mathrm{true}}|f^*]

= (\mathbb{P}[\beta_{\mathrm{true}} > \rho_f^{-1}(T)_u|\beta^*] + \mathbb{P}[\beta_{\mathrm{true}} < \rho_f^{-1}(T)_l]|\beta^*)\mathbb{P}[f_{\mathrm{true}}|f^*]

These terms need to be integrated over f_{\mathrm{true}}, but for whatever reason the wordpress parser doesn’t like it when I put $\int_{f_{\mathrm{true}}$ into the above equations. And in practice, for even rare variants on the order of 0.5% frequency, the posterior frequency estimate is peaked enough to be well-approximated by setting f=f^* (remembering, of course, that all frequencies are population-based, so oversampling cases requires re-adjusting the observed frequency based on the prevalence of the disease: f = (1-p)f_U + pf_A).

The last thing to work out is the function \rho(\beta,f,\mathrm{prevalence}) giving the phenotypic variance explained by a variant of frequency f, effect size \beta on a dichotomous trait of a given prevalence. It’s very well known how to compute the liability-scale variance, and the inverse can be found trivially through numerical quadrature.

Liability-scale Variance: A Derivation

Recent discussions have left me slightly cynical on the common intuition behind this calculation (an intuition which seems to be “cite So et al 2012”), so it may be worth stepping through the derivation. Let’s start with a disease, and a variant. The diesease is 10% prevalence, and the variant has a 10% frequency, and an odds ratio of 1.35 (so \beta = 0.30). We begin with assuming an underlying latent variable with some distribution, and for the sake of having a pretty function, I’m going to assume a logistic. There’s also a choice between setting the mean of latent variable (over the population) to 0, and letting the threshold T adjust, or setting T=0 and letting the mean adjust. I will do the latter. So basically we have a whole population that looks like


Where the area under the curve to the right of 0 is 0.1. The population mean is exactly \mu_P = -\log(1/r-1). So the question is: whereabouts in this liability scale do carriers fall? For that we need to know the probability of being affected by genotype state. Given the odds ratio, this is pretty easy:

\mathbb{P}[A|X=2] = \left[1 + \exp(\mu_R + 2\beta)\right]^{-1} = \left[1 + \exp(\mu_R + 0.6)\right]^{-1} = P_V

\mathbb{P}[A|X=1] = \left[1+\exp(\mu_R + \beta)\right]^{-1} = \left[1+\exp(\mu_R+0.3)\right]^{-1} = P_H

\mathbb{P}[A|X=0] = \left[1+\exp(\mu_R)\right]^{-1} = P_R

\mathbb{P}[A] = \mathrm{Prevalence} = \left[(1-f)^2P_R + 2f(1-f)P_H + f^2P_V\right]

There are three equations and three unknowns (plug in \mu_R = -\log(1/P_R-1)), and so this system is soluble. This can be reduced easily to a single equation by plugging in, and solved by a simple root solver such as

diseaseProbs <- function(frequency,odds,prevalence) {
bt <- log(odds)
cPrev <- function(muR) {
PR <- (1-frequency)^2*logistic(muR)
PH <- 2*frequency*(1-frequency)*logistic(muR + bt)
PV <- frequency^2*logistic(muR+2*bt)
(PR + PH + PV - prevalence)
if ( odds > 1.05 ) {
# prevalence almong reference individuals will be lower
res <- uniroot(cPrev,lower=invlogistic(0.001),upper=invlogistic(prevalence))
} else if ( odds < 0.95 ){
# prevalence among reference individuals will be higher
res <- uniroot(cPrev,lower=invlogistic(prevalence),upper=invlogistic(0.99))
} else {
upr <- invlogistic(min(1.2*prevalence,1-1e-5))
res <- uniroot(cprev,lower=invlogistic(0.8*prevalence),upper=upr)
muR <- res$root

So what does this give us? Well it gives us the Logistic Mixture comprising the population distribution

Where I haven’t been entirely faithful to the densities (I’m scaling by the square root of the frequencies of the genotypes). Point is, you can see the shift in the distributions by genotype, and consequently the proportion of the distribution curves falling above the T=0 threshold. At this point, we can just plug into the formula for variance: \mathbb{E}[(X-\mathbb{E}[X])^2] to get

V = (1-f)^2 (\mu_P-\mu_R)^2 + 2f(1-f)(\mu_P-\mu_R-\beta)^2 + f^2(\mu_P-\mu_R-2\beta)^2

Of course throughout we have assumed a standard Logistically distributed error term. Thus the variance of the means have to be given to us as a proportion of the total variance, or in other words \rho(\beta,f) = \frac{\sigma_g^2}{\sigma_g^2+\sigma_e^2}. In this case, the variance of the logistic is \pi^2/3, and thus we set

\rho = \frac{V}{\pi^2/3 + V} = \frac{0.016}{3.28+0.016} \approx 0.0049

So roughly 0.5% of the liability-scale variance. Note that using the standard method of replacing the logistic distribution with a standard normal, and using \rho_{\mathrm{norm}} = \frac{V_{\mathrm{norm}}}{1+V_{\mathrm{norm}}} results in an estimate of 0.44%. These differences increase with the variance explained, so that for a 20% frequency variant with OR=2.35, such a variant explains roughly 6% in the logistic model, but 5% variance in the normal model.

Assuming the posterior distribution of f is sufficiently peaked, doing a GWAS-like bounding scan is fairly simple. For each variant, calculate

(\beta_u,\beta_l): \rho(\beta,f_i) = T

via \rho_{f_i}^{-1}(T). Then, using the posterior distribution of d\mathbb{P}[\beta_\mathrm{true}|X,C_1,\dots] calculate

p_i = \Phi(\beta_l/\sigma_\beta)+(1-\Phi(\beta_u/\sigma_\beta)).

Multiple Test Considerations

Where does the figure 1e-7 come from for GWAS studies? Or 5e-8 for sequencing studies? (And I mean conceptually, not here here or here). The basic logic is that of the look elsewhere effect:

1) Most variants are null

2) There are lots and lots of variants

3) There are many chances to see spurious nominal associations

4) Must set the threshold fairly high to achieve a study-wide Type-I error of 5%.

The fundamental consideration is (1), and there’s a significant asymmetry between a GWAS scan to reject \beta = 0, and a bounding scan to reject \beta \not \in (\beta_l,\beta_u). If most variants are null under a GWAS scan and ought not to be rejected, then almost no variants are null under a bounding scan, so most ought to be rejected. That is: Type-I error is bad in a GWAS scan (you find something that’s not real), and you’re willing to pay a cost of Type-II error (you don’t find something that is real). By contrast, for a bounding scan, Type-II error is bad (you put bounds on a truly causal variant), while Type-I error is less of an issue (you fail to bound a noncausal variant).

Thus, previous conversations about multiple testing are not applicable, and one shouldn’t blindly apply p=5e-7. Instead, bounding requires a good deal more thought (or assumption) about the architecture of the trait. I would articulate the logic as

1) Causal variants are null

2) Few variants are null

3) There are lots and lots of variants

4) There are many chances to falsely accept the null

5) We can be rather aggressive on the rejection p-value

It’s worth articulating why we don’t care all that much about false rejects: rejecting the null falsely simply includes a non-causal variant in a set of variants that should be enriched for causal variants. Variants for which the correct test is to reject \beta = 0. And it’s absolutely possible for a variant to be such that (e.g. have a large enough standard deviation that) H_0: \beta = 0 is rejected, as well as H_0: \beta \not \in (\beta_l,\beta_u) is rejected. On the other hand, failing to reject the null on a causal variant means we can potentially exclude it from follow-up analyses, a situation we want to avoid.

So there’s a different balance between Type-I and Type-II error here, with Type-II being the one we’re concerned about. But of the two, Type-II error is the trickier, because it’s fundamentally a question of power. The idea is, well, we don’t want to accidentally exclude things. But you have to be a little bit more specific: what kind of things do you not want to exclude? You can be sensitive to all causal variants (even those with OR=1+1e-5) by rejecting everything. So being more reasonable, you might say “I want no false acceptances of any variant with >0.5% of phenotypic variance explained”. Given that statement, you can calculate the power w(\rho=0.05,p_{\mathrm{nom}}), and that’s the power at the nominal threshold p_{\mathrm{nom}}. (See previous posts regarding calculation of power). But of course, that’s not quite enough, because you also need to know the number of chances to falsely accept such a variant, which is, of course, begging the question (if you knew how many causal variants there were, why bother with the exercise?). One way to get around this is to simply assume an unreasonable number of causal variants of such variance explained, N_{\mathrm{UB}} and then use the same machinery as Bonferroni correction and set

p_{\mathrm{nom}} : 1-(1-w(0.05,p_\mathrm{nom}))^{N_\mathrm{UB}} = 0.01

Bounding Variance Explained at a Locus

Alright, so that all was about variants you know about. But what if you care about a specific locus, like a gene, and want to know if variants within that gene contribute substantially to heritability. There are several different questions to articulate, but for now let’s stick with the single-variant approach. We know, from the previous section, how to answer “what is the probability that one of the variants in this locus explains a T or greater portion of phenotypic variance?”

But now we’ll take a step into the unknown. The second-order question: what is the probability that no variant exists at this locus that explains a T or greater proportion of phenotypic variance? That is, given I’ve sequenced the locus and haven’t found anything, what’s the probability I could keep on sequencing and still wouldn’t find anything?

Well, what’s the probability the sun will rise tomorrow?

Following Laplace, 9592/9593.

Well Okay. In all seriousness, this particular question about genetic mutation has just enough structure in it to avoid the philosophical issues that arise with the Sunrise Problem (Statistics can’t prove a negative, etc). Specifically: we rely on the fact that we’ve done sequencing. This means that we have not failed to query sites for mutations (as in the case of genotype chips), but we have, and there were none. That is, if a variant exists, we’ve got a pretty good idea about it’s frequency. Let’s turn to Mister Bayes, and ask, given I’ve sequenced N samples and seen \alpha counts of a given allele, what is the posterior density of the allele frequency? Using the Rule:

d\mathbb{P}[p|\alpha;N] = \frac{ [x^\alpha] (px + q)^{2N} d\mathbb{P}[p]}{\int_p [x^\alpha] (px + q)^{2N} d\mathbb{P}[p]} = \frac{{2N \choose \alpha} p^\alpha(1-p)^{2N-\alpha}d\mathbb{P}[p]}{\int_p{2N \choose \alpha} p^{\alpha}(1-p)^{2N-\alpha}d\mathbb{P}[p]}

This doesn’t give a good intuitive sense of the posterior distribution other than the basic shape (gamma-like, no?). The best thing to use as a prior is the allele frequency spectrum modeled on the human bottleneck-and-superexponential-expansion (see Evans and Shvets, for instance), but I find a good intuitive model (that surprisingly works well in practice) is a truncated inverse distribution

d\mathbb{P}_\epsilon[p] = \left[-p\log(\epsilon)\right]^{-1}

which is distributed on the domain (\epsilon,1]. This tends to overestimate allele frequency because (1) humans have grown faster than exponentially, and (2) no mutation is allowed to have a frequency lower than \epsilon. You can make a Gamma distribution peak at \epsilon and then go to 0, but this is a nice toy distribution. Plugging it in yields

{2N \choose \alpha} p^{\alpha-1}(1-p)^{2N-\alpha} \left[\int_\epsilon^1 {2N \choose \alpha} p^{\alpha-1}(1-p)^{2N-\alpha}dp\right]^{-1}

Digression: The Probability that a Singleton is more than a Singleton

This is actually a fun little proof I have given this simplified prior. You go out and sequence N people, and find a singleton you care about. What’s the probability that it’s frequency is >1/2N? I’ll prove that it’s about \frac{1}{e}. What’s the denominator of the above formula when \alpha = 1? Plugging in

\int_\epsilon^1 \frac{2NZp(1-p)^{2N-1}}{p}dp = \int_\epsilon^1 2NZ(1-p)^{2N-1}dp = Z(1-\epsilon)^{2N}

And therefore the conditional posterior of f can be written

d\mathbb{P}[f \geq p | \mathrm{AC=1\; in \;} N] = \frac{2NZp(1-p)^{2N-1}}{Zp(1-\epsilon)^{2N}} = \frac{2N(1-p)^{2N-1}}{(1-\epsilon)^{2N}}

Now we can inquire as to the probability that, given AC=1 in N people, the true frequency will be greater than some value \delta. This is:

\int_\delta^1 \frac{2N(1-p)^{2N-1}}{(1-\epsilon)^{2N}}dp = \left(\frac{1-\delta}{1-\epsilon}\right)^{2N}

Now let \delta = \epsilon + \delta':

= \left(\frac{1-\epsilon-\delta'}{1-\epsilon}\right)^{2N} = \left(1 - \frac{\delta'}{1-\epsilon}\right)^{2N}

Letting \delta' = \frac{1}{2N} - \epsilon yields:

\mathbb{P}[f \geq \frac{1}{2N}-\epsilon | \mathrm{AC = 1 \; in \;} N] = \left(1-\frac{1}{2N(1-\epsilon)}\right)^{2N} \longrightarrow \exp\left[-\frac{1}{1-\epsilon}\right] \approx e^{-1}

Anyway, the point is you have some posterior estimate f_{\mathrm{post}}(p) of the allele frequency spectrum given that you haven’t observed it in your sequencing. Any variant you haven’t seen yet has that posterior spectrum, and thus given a fixed proportion of phenotypic variance explained T, the odds ratios that such sites must have are constrained to be very large. In particular, for a 10% prevalence disease, using the above model, a 0.01% frequency variant would need an odds ratio of 400,000 to explain 1% of the liability-scale variance.

However, the fact that for such a rare variant, 1% phenotypic variance is achievable is really a breakdown of the liability-scale model. In particular, there is a ceiling on the variance explained by a mutation: a 0.01% variant that is fully penetrant only explains 0.1% of the prevalence of the trait. That is, at some point you know that any undiscovered single variant left at a locus, even if fully penetrant, cannot explain a significant fraction of the phenotypic variance.

On the observed (0/1) scale, such a variant of frequency f for a disease of prevalence p explains a f(1-f)/K(1-K) proportion of the phenotypic variance. Transferring this to the liability scale by Dempster’s formula

h_{0/1} = t^2h_x/(pq) = t^2 h_x / [K(1-K)]

Now the genetic variance on the observed scale, \sigma_{g_{0/1}}^2 = \beta f(1-f) \leq f(1-f) as the slope is at most 1. \sigma_{p_{0/1}}^2 = K(1-K) by definition, and therefore h_{0/1} \leq f(1-f)/K(1-K). Obviously during the conversion to the liability scale, the phenotypic variance, which appears in both denominators, will cancel. Thus we have (for prevalence K):

f(1-f) = t^2h_x \Rightarrow h_x = f(1-f)/t^2.

Here, t = \phi(\Phi^{-1}(1-K)) = \phi(1.28) = 0.17 so for f = 0.0001 and 8% prevalence, h_x = 0.0045 or 0.45% of the phenotypic variance. This is a bit of a tawdry estimate, as such a variant equipped with OR=15 explains (by the other model) 0.14% of the phenotypic variance.  Nevertheless, this transformation provides a reasonable approximation to an upper bound for rarer variants (but we should still search for better corrections to it). Thus, denoting by

\rho(f) = f(1-f)/\phi(\Phi^{-1}(1-K))^2

the function mapping a frequency to the maximum liability variance explained (e.g. that when the variant is fully penetrant), the probability that an undiscovered locus explains \geq T fraction of phenotypic variance is

\mathbb{P}[V \geq T] = \int_f \mathbb{P}[\rho(f) > T | f]f_{\mathrm{post}}(f) < \int_{f_\mathrm{min}}^1 f_{\mathrm{post}}(x)dx < (1-f_\mathrm{min})f_{\mathrm{post}}(f_{\mathrm{min}})

where f_{\mathrm{min}} is the minimum f such that \rho(f) > T. Note that this expression is also < f_\mathrm{post}(f_{\mathrm{min}}), that is, bound by the posterior allele frequency distribution function evaluated at f_\mathrm{min}.

Now f_\mathrm{min} is easy to calculate, set V =f(1-f)/\phi(\Phi^{-1}(1-\mathrm{prev}))^2 = zf(1-f) so that

f_\mathrm{min} = \frac{1}{2} \pm \frac{1}{2z} \sqrt{z^2 - 4Vz}

Thus given the prevalence of a disease, there is an effective upper bound on the liability-scale variance explained, given that the observed 0/1 variance cannot exceed f(1-f). Here, we plot f_{\mathrm{min}} as a function of the variance explained



So let’s go to our example. Lets say you’ve got a 10% prevalence disease, and have sequenced 50,000 individuals at a locus. You want to know the probability that there’s a 1% variance explained mutation hiding somewhere in your population that you didn’t discover. Then V=1% and z = 0.17, plugging in gives f_\mathrm{min} = 0.00034. Using the posterior from above, f_\mathrm{post}(f_\mathrm{min}) < 1.5\times 10^{-16}. Here’s the kicker: Even if you’ve sequenced only 10,000 individuals. So long as you haven’t seen a variant at all, the chance that such variant that could explain 1% of the variance is still < 1e-11. That means that for a 1e-6 “chance” to have missed such a variant, about 100,000 such variants would have to exist in the population you sampled. At the locus you’re looking at. Quite reasonable on a genome-wide scale. Quite unreasonable for a gene.

In other words, if even a moderate amount of sequencing has been done on your gene, there are no more single variants left to find.

At least, if you care about single variants explaining a large portion of heritability. Other caveats: this assumes a homogenous population, it could be that there are populations where such variants do exist even at reasonable frequencies.

But wait, there’s more. Let’s say such a variant does exist. It’s completely penetrant, but it has a frequency of f < 1/20,000. For the sake of example, let’s say you’ve sequenced people from Dublin, and this variant at frequency 1/50,000 didn’t get into your study. Or maybe you did see a copy or two, it actually doesn’t matter. Suppose it’s causal dominant, you get the disease if you’re a carrier.

But here’s the deal. Dublin’s population is 1.3 million. Only 26 copies of this allele exist. You could sequence every person in Dublin and you wouldn’t have the power to associate it at 5e-7. Furthermore, there are constraints beyond population size: you need to actually collect the samples, and you need to pay for the sequencing. Thus, in addition to there not being single variants of high variance explained left to find, many of those things we haven’t found yet cannot be demonstrably associated. They are un-followupable.

The good news is, the things we have found can. But at some point the posterior allele frequency becomes so scrunched towards 0 that (on a single-variant level at least) you just have to forget about ever following those up statistically. At that point you’ve got to break out the crispers and engineer some cells.

Another Comment on Studies

The preceding discussion is basically the entirety of the reason sequencing studies have really dropped the ball regarding the genetic architecture of the traits they examine. Sequencing studies are effectively mini-GWAS studies, characterized by a Q-Q plot and a multiple-testing burden higher even than that of GWAS, with no clear understanding or mention of why sequencing was undertaken in the first place. “We wanted to discover all the variants present in our gene.” Okay fine. Given you’ve done that, do we ever need to sequence that gene again? What’s the probability that we missed something there that’s explaining a large fraction of the variance of the phenotype? You don’t even need phenotyped samples to answer that question, you can just use estimates from the 1000 Genomes Project!

This is what’s frustrating: genetic studies cherry-pick one or two novel top hits, and leave everything else on the table. The process of exclusion has been entirely ignored. If we went back, and actually analyzed the data with a careful eye, we probably would have completely excluded hundreds, maybe thousands of loci from consideration. Certainly thousands of single variants.

The Multi-Variant View

My little (now reaching ~3500 words) invective, up til now, has been focused on a single-variant view of heritability (variance explained). This view, while helpful for talking about what can be true about the properties of single variants, is less helpful about talking about what can be true about sets of variants. Things like “variants in SOX9” (a very cool gene), or “variants in open chromatin regions near actively transcribed genes in renal cells.” This section is basically an extension of the previous discussion to groups of variants; but this alteration presents some novel challenges: the nonlinearity of heritability estimates, the large state space of multi-variant genotypes, and the statistical brutality of linkage disequilibrium.

Expanded Multivariant View

Now, rather than having a single variant \nu, one has multiple variants \nu_1,\dots,\nu_n, with frequencies f_i, and effects \beta_i. It’d be very nice (and indeed, some papers do) to write

\rho(\vec \nu) = \sum_{i=1}^n \rho(\beta_i,f_i)

But unfortunately \rho is linear neither in \beta nor in f. First, \rho = V/(\sigma_2^2 + V) is decidedly nonlinear in V. Second, V is quadratic in both f and \mu, and \mu is quadratic in f and inverse logistic in \beta. So forget that sum. Instead, it is straightforward to extend from a genotype to a multigenotype.

Multiple Variant Variance Explained

This follows from replacing the index (Ref,Het,Var) from the previous calculation with the multi-index ([Ref,Ref,…],…,[Var,Var…]). For convenience, we’ll wrap the multi-index to a univariate index i \in (0,\dots,3^n), and denote by G_j \in i the genotype of the jth variant in the ith multigenotype. Then:

\mathbb{P}[A|i] = [1+\exp(\mu_0 + \sum_{G_j \in i} G_j\beta_j)]^{-1} = P_i(\mu_0)

The frequency of multigenotype i we denote by F_i, which, in the case of full HWE with no LD is

F_i = \prod_{G_j \in i} \binom{2}{G_j} f_j^{G_j}(1-f_j)^{2-G_j}

\mathrm{Prevalence} = \sum_{i=0}^{3^n} P_i(\mu_0)F_i

Then using \mu_T = -\log(1/\mathrm{Prev}-1)

V = \sum_{i=0}^{3^n} (\mu_i-\mu_t)^2F_i

\rho = \frac{V}{\pi^2/3 + V}

The only issue is the sum. As in the case of power (which requires massive sums over genotype space), we can get around this more efficiently via simulation. We can exploit the fact that we can set \mu_0 = 0 and allow T to shift. It’s easier also to use the standard normal rather than the logistic for this (as a sum of normals is still normal) A simulation would then be:

multiVarSim <- function(frequency,odds,prevalence,logit=T,prec=0.01) {
bt <- log(odds)
invlink <- qnorm
link <- pnorm
if ( logit ) {
invlink <- invlogistic
link <- logistic
# this part can be done with replicate, but I enjoy vector algebra
nRuns = round(10/prec,1)
drawGeno <- function(f) { rbinom(nRuns,size=2,prob=f) }
S <- as.matrix(sapply(frequency,drawGeno)) %*% as.matrix(bt)
# now u_0 needs to be such that the total prevalence is prevalence
# this means that sum(link(S+u0))/length(S) = prevalence
cPrev <- function(muR) {
sum(link(S+muR))/length(S) - prevalence
res <- uniroot(cPrev,lower=invlink(0.001),upper=invlink(0.999))
muR <- res$root
S <- S + muR
# now remember we care about the variance around muP
sum((S - invlink(prevalence))^2)/length(S)

The only trouble with using the multi-genotype approach is that the state space is huge: for n variants, there are 3^n genotype assignments, so forget about looking at 15 variants, let alone hundreds. As mentioned, simulation can overcome this setback, but simulations themselves are expensive.

But even beyond that, when one moves from calculating variance explained by several variants to bounding variance explained by several variants, the numerics becomes challenging. In particular, one moves from a one-parameter posterior distribution (two-parameter if taking uncertainty of the frequency into account) to an n-parameter distribution (2n if accounting for frequency uncertainties), with non-axial limits of integration. That is, while for a single variant

\rho_f^{-1}(V)_u produced a single point \beta_u : \rho(\beta_u,f) = V, for multiple variants

\rho_f^{-1}(V)_u produces a curve: \beta_{u_i} : \rho(\beta_u, f) = V

That is, you can reduce the effect size of one variant, while increasing the effect size of another variant to compensate. This is a situation where one might use Monte Carlo simulation to evaluate the integral: but note that for each point of the Monte Carlo, a simulation needs to be run to get the variance explained. This is terribly costly.

Another way to bound the probability is to solve the constrained optimization

\mathrm{max} -\log \mathbb{P}[\vec \beta_{\mathrm{true}} = \vec \beta_u | \beta^*,f]

s.t. \;\; \rho(\beta_u,f) = V

The likelihood is (luckily) convex, so this isn’t excessively difficult to do. Let p^* be that maximal p-value. Then

\mathbb{P}[V_{\mathrm{true}} > V | \beta^*,f^*] \leq 1-\Phi(\phi^{-1}(1-p^*))

Nevertheless, even this is very costly. For every evaluation of \rho by the optimizer, a simulation needs to be done to estimate its value; even this approximation is really expensive. In addition, LD generates additional difficulty: Haplotypes need to be simulated rather than genotypes (in order to estimate \rho), and if the \beta^* were fit independently rather than jointly, both the mean and the the variance-covariance matrix of the posterior distribution need to be adjusted to account for LD.

This, combined with the problem of estimating effect sizes from low-frequency variants, leads to methods of collapsing variants across a locus into scores.

Collapsed Multivariant View

Collapsing is a means of re-writing the multiple-variant joint model. Instead of

\mathrm{lgt}(Y) = \sum_i \beta_i X_i + \sum_i \gamma_i C_i + \alpha

we write X as a matrix and have

\mathrm{lgt}(Y) = \tau X\xi + \sum_i \gamma_iC_i + \alpha

Where \xi_i is constant and for the calculation of variance explained, \xi_i = \beta_i. The point is \xi itself is not fit, but only the coefficient \tau which, when \xi = \vec\beta, \tau=1. Collapsing tests (“burden” tests) don’t have access to \beta_i, but instead try to “guess” using some function \xi = \Xi(\vec \nu) of the variant properties (like frequency, estimated deleteriousness, and so on).

One thing immediately recognizable is that if \xi = \vec \beta and \tau = 1 then the formula for

\mathbb{P}[A|i] = [1+\exp(\mu_0 + \sum_{G_j \in i} \beta_i G_j)]^{-1} = [1 + \exp(\mu_0 + \vec G_i^{\dagger} \xi)]^{-1}

So in other words, the score vector \vec S = \tau X\xi is an estimate of the latent liability variable for all of the samples. This allows the following simplifying assumption:

S_i \sim N(\mu,\sigma^2)

for some \mu and \sigma. This is sort of more-or-less true as X_{\cdot,j} are a sequence of binom(2,f_i) variables, and so a weighted sum should be approximately binomial, ergo approximately normal. Therefore, for a given \tau, \xi:

Variance Explained by a Collapse Test

We have \mathbb{P}[A|S] = 1-\Phi(\mu_0-\tau S). Here we use a normal latent model because it plays nicely with the assumption that S is normal. Then

\mathrm{Prevalence} = \int_{T}^\infty (1-\Phi(\tau S))\phi((\tau S - \mu_{\tau S})/\sigma_{\tau S}) dS

As before, T can be found by numerical quadrature. Then

V = \mathrm{var}(T - \tau S)

and \rho(S,\tau) = V/(1+V).

Note that this can be simplifed by talking about a variable R = \tau S, but it’s nice to clarify what \tau does (which is scale the proposed score distribution so it aligns with the underlying liability explained).

To use this as an approximation to the variance explained by multiple variants, note that S is a linear function, and therefore (assuming no LD and no relatives):

\mathbb{E}[S] = \mathbb{E}[X\xi] = \mathbb{E}[X]\xi \rightarrow \mathbb{E}[S_i] = \sum_j 2f_j\beta_j

\mathrm{Var}[S_i] = \sum_j \beta_j^2 f_j(1-f_j)

Expressions which can be adapted for the presence of LD and relatedness.

This gives \mu_{\tau S} = \tau \sum 2f_j\beta_j and \sigma^2_{\tau S} = \tau^2 \sum \beta_j^2 f_j(1-f_j)

For an evaluation of “true” variance explained, set \tau = 1. To identify the variance explained by a (possibly wrong) guess \xi, replace all instances of \beta_j with \xi_j.

Using a collapsed estimate of the variance explained has the benefit of being univariate. That is, for a given (either guess or true) \xi, then \rho = \rho_\xi(\tau,f), and thus it has a univariate inverse: \rho_{\xi,f}^{-1}(\rho) = (\tau_l,\tau_u).  This enables the bounding of a locus or burden test through the posterior distribution of the parameter \tau, just as we did with a univariate \beta in the first section. That is, given \xi (and assuming we don’t need to integrate over the posterior of f_i which is fairly painful in this case), to query the probability of a locus explaining Q or more of the phenotypic variance:

Calculate (\tau_l,\tau_u) = \rho_{\xi,f}^{-1}(Q)

Calculate p = \Phi( (\tau_l-\tau^*)/\mathrm{SE}_\tau ) + 1-\Phi( (\tau_u - \tau^*)/\mathrm{SE}_{\tau})

However (!), the obvious approach (set \xi_i = \beta^*_i) where \vec \beta was fit jointly by MLE has the drawback that \tau is inflated due to overfitting. In fact, in such cases \tau=1 always. One way around this is to use \beta_i estimated from a different source. Alternatively let \xi be a hypothesized score (e.g. a burden weight vector). It’s important to note in the latter case that bounding variance explained by a burden test does not bound the maximum possible variance explained at a locus, it bounds the variance explained by the hypothesized \xi. The variants at the locus could still contribute substantially to trait heritability, just simply in a direction orthogonal to \xi (of which there are n-1).

Surely the many things I haven’t seen explain lots of heritability in bulk, right? Right?

The last thing to check off with the locus view now that we can bound variance explained by (1) multiple variants and (2) burden scores, is the probability that at said locus, there may exist many variants that for whatever reason were not discovered, but that in aggregate explain a large proportion of heritability. As in the single-variant case, you can put bounds on these things, but more importantly, consider what it means to want the answer to this question (as anything more than an exercise in probability).

It’s been a long post. Let’s take a step back.

Human medical genetics is science with an ulterior motive, where the search for additional causal variants is often explicitly motivated by the statement that new loci provide new targets for pharmaceutical treatments. And, by and large, this is a positive force for the advancement of disease biology and the understanding of human disease. At the same time, I believe that this Quest For Treatment, combined with the increasing focus on impact explains a wide variety of phenomena in the medical and statistical genetics community, from hasty and opportunistic study design to the ENCODE backlash (and the resurgence of Big vs Small science).

Sequencing is a good example. Initial GWAS studies provided a good number of variants and loci with strong disease associations. The bulk of these associations, however, were not immediately interpretable: falling between genes (unclear which protein might be affected), or in a noncoding part of a gene (so not obviously gain- or loss-of-function). In part because of the difficulty of interpreting biological effects, and in part because of the worry of a winner’s-curse effect, we started (rather uncritically) to refer to these variants as “tag-SNPs”, hypothesizing that the true causal variant was unlikely to have been ascertained, as the bulk of human variation is uncommon to rare and not present in the set of imputed loci, and furthermore is likely to have an interpretable biological impact. In retrospect, it seems rather clear that common variants which maintain their association across populations are unlikely to be tagging a “true causal variant” of lower frequency which is far more likely to be absent in other populations. (That said, one  proof of an elegant experiment that the results reveal something that is obvious in retrospect)

I think the shift from array-based GWAS towards sequencing-based studies reflects both the optimism of researchers, and the entrance of impact as a scientific consideration. Should loss-of-function mutations underlie even 10% of the GWAS hits, we’d then have generated a respectable number of druggable targets, opening up new paths towards treatment. Even having seen the (largely negative) results, even as I agree with Kirschner’s characteriztion of impact, I still think these were the right designs to follow up on the results of GWAS.

But what it does mean is that these studies weren’t designed to add to the knowledge of genetic architecture. Why didn’t we only sequence cases that had none (or very few) of the known genetic risk factors? Because at the same time we wanted to see if there were un-discovered variants underlying those GWAS signals. Why do we sequence exomes instead of the regions near GWAS hits? Because not only do many GWAS loci fall near to or within genes, but also protein-coding variants, in particular loss-of-function variants, provide a very clear target for both follow-up lab experiments, and potential therapeutic developments. In addition, exome sequencing is cheaper so one can sequence more samples to find more rare variants and have more power to associate them.

So, really, the question “What’s the likelihood that there are multiple variants that I have yet to ascertain that in aggregate explain a substantial fraction of phenotypic variance?” is a continuation of this rather incautious optimism about 1) the strictly additive model holding, and 2) the infinitesmal (“Quantiative”) model not holding, to say nothing of 3) unbiased estimates of heritability. For a common disease, there are reasons on all three fronts to cautiously articulate hypotheses before going any further in the Quest for Treatment.

As mentioned in the last section on bounding the variance explained by undiscovered variants, we’ve now gotten to territory where undiscovered variants are so rare that in order to explain even 0.1% of the phenotypic variance they have to be effectively 100% penetrant. The fact that common diseases are not known to present as Mendelian in a substantial portion of cases, as the assumption that extremely rare (or private) variants of strong effect would suggest, indicates that such variants are not likely to account for a large fraction of disease prevalence. At the same time if these variants are not of high effect but together account for a large fraction of heritability, the model isn’t really distinguishable from the Quantitative model: every variant is causal, the effect size is negligible.

At the same time, the Latent Variable Model is just an approximation, and while it alleviates some of the issues of treating a binary trait as a real-valued trait (with actual values of 0 and 1), it does not eliminate them. That is, phantom epistatic effects are mitigated, but not not eliminated (because the latent variable need not be normal, though we assume so). This not only impacts estimates of heritability, but also indicates that the purely additive model is mis-aligned, and there might be a considerable gain (in terms of understanding heritability estimates) to carefully considering what happens in individuals with many genetic risk factors. At the same time, both association scans and association study experimental designs tend not to consider maternal, dominance, additive-additive, or additive-environment effects. Which seems like a more fruitful use of research money: sequencing many thousands of samples in the hope of finding a fully penetrant f=1/30,000 variant, or collecting a wide array of phenotypes and environmental data to better understand endogenous and exogenous disease and gene x disease covariates? Or buying a cluster (or access to Amazon’s) to scan for additive-additive effects?

In sum: none of this proves that a locus can’t harbor undiscovered variants that explain some given fraction of phenotypic variants. One can bound that probability just as in the single-variant section. But the point is: think about why such a bound is necessary. Is the working hypothesis to be tested really that there are high-penetrance near-private variants lurking in the genome? Is that really the hypothesis Occam’s Razor would suggest, given all of the observations in this post?

I, for one, don’t think so.

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