did variational Bayes work?

An interesting ICML 2018 paper by Yuling Yao, Aki Vehtari, Daniel Simpson, and Andrew Gelman I missed last summer on [the fairly important issue of] assessing the quality or lack thereof of a variational Bayes approximation. In the sense of being near enough from the true posterior. The criterion that they propose in this paper relates to the Pareto smoothed importance sampling technique discussed in an earlier post and which I remember discussing with Andrew when he visited CREST a few years ago. The truncation of the importance weights of prior x likelihood / VB approximation avoids infinite variance issues but induces an unknown amount of bias. The resulting diagnostic is based on the estimation of the Pareto order k. If the true value of k is less than ½, the variance of the associated Pareto distribution is finite. The paper suggests to conclude at the worth of the variational approximation when the estimate of k is less than 0.7, based on the empirical assessment of the earlier paper. The paper also contains a remark on the poor performances of the generalisation of this method to marginal settings, that is, when the importance weight is the ratio of the true and variational marginals for a sub-vector of interest. I find the counter-performances somewhat worrying in that Rao-Blackwellisation arguments make me prefer marginal ratios to joint ratios. It may however be due to a poor approximation of the marginal ratio that reflects on the approximation and not on the ratio itself. A second proposal in the paper focus on solely the point estimate returned by the variational Bayes approximation. Testing that the posterior predictive is well-calibrated. This is less appealing, especially when the authors point out the “dissadvantage is that this diagnostic does not cover the case where the observed data is not well represented by the model.” In other words, misspecified situations. This potential misspecification could presumably be tested by comparing the Pareto fit based on the actual data with a Pareto fit based on simulated data. Among other deficiencies, they point that this is “a local diagnostic that will not detect unseen modes”. In other words, what you get is what you see.

priors without likelihoods are like sloths without…

“The idea of building priors that generate reasonable data may seem like an unusual idea…”

Andrew, Dan, and Michael arXived a opinion piece last week entitled “The prior can generally only be understood in the context of the likelihood”. Which connects to the earlier Read Paper of Gelman and Hennig I discussed last year. I cannot state strong disagreement with the positions taken in this piece, actually, in that I do not think prior distributions ever occur as a given but are rather chosen as a reference measure to probabilise the parameter space and eventually prioritise regions over others. If anything I find myself even further on the prior agnosticism gradation.  (Of course, this lack of disagreement applies to the likelihood understood as a function of both the data and the parameter, rather than of the parameter only, conditional on the data. Priors cannot be depending on the data without incurring disastrous consequences!)

“…it contradicts the conceptual principle that the prior distribution should convey only information that is available before the data have been collected.”

The first example is somewhat disappointing in that it revolves as so many Bayesian textbooks (since Laplace!) around the [sex ratio] Binomial probability parameter and concludes at the strong or long-lasting impact of the Uniform prior. I do not see much of a contradiction between the use of a Uniform prior and the collection of prior information, if only because there is not standardised way to transfer prior information into prior construction. And more fundamentally because a parameter rarely makes sense by itself, alone, without a model that relates it to potential data. As for instance in a regression model. More, following my epiphany of last semester, about the relativity of the prior, I see no damage in the prior being relevant, as I only attach a relative meaning to statements based on the posterior. Rather than trying to limit the impact of a prior, we should rather build assessment tools to measure this impact, for instance by prior predictive simulations. And this is where I come to quite agree with the authors.

“…non-identifiabilities, and near nonidentifiabilites, of complex models can lead to unexpected amounts of weight being given to certain aspects of the prior.”

Another rather straightforward remark is that non-identifiable models see the impact of a prior remain as the sample size grows. And I still see no issue with this fact in a relative approach. When the authors mention (p.7) that purely mathematical priors perform more poorly than weakly informative priors it is hard to see what they mean by this “performance”.

“…judge a prior by examining the data generating processes it favors and disfavors.”

Besides those points, I completely agree with them about the fundamental relevance of the prior as a generative process, only when the likelihood becomes available. And simulatable. (This point is found in many references, including our response to the American Statistician paper Hidden dangers of specifying noninformative priors, with Kaniav Kamary. With the same illustration on a logistic regression.) I also agree to their criticism of the marginal likelihood and Bayes factors as being so strongly impacted by the choice of a prior, if treated as absolute quantities. I also if more reluctantly and somewhat heretically see a point in using the posterior predictive for assessing whether a prior is relevant for the data at hand. At least at a conceptual level. I am however less certain about how to handle improper priors based on their recommendations. In conclusion, it would be great to see one [or more] of the authors at O-Bayes 2017 in Austin as I am sure it would stem nice discussions there! (And by the way I have no prior idea on how to conclude the comparison in the title!)

Goodness-of-fit statistics for ABC

“Posterior predictive checks are well-suited to Approximate Bayesian Computation”

Louisiane Lemaire and her coauthors from Grenoble have just arXived a new paper on designing a goodness-of-fit statistic from ABC outputs. The statistic is constructed from a comparison between the observed (summary) statistics and replicated summary statistics generated from the posterior predictive distribution. This is a major difference with the standard ABC distance, when the replicated summary statistics are generated from the prior predictive distribution. The core of the paper is about calibrating a posterior predictive p-value derived from this distance, since it is not properly calibrated in the frequentist sense that it is not uniformly distributed “under the null”. A point I discussed in an ‘Og entry about Andrews’ book a few years ago.

The paper opposes the average distance between ABC acceptable summary statistics and the observed realisation to the average distance between ABC posterior predictive simulations of summary statistics and the observed realisation. In the simplest case (e.g., without a post-processing of the summary statistics), the main difference between both average distances is that the summary statistics are used twice in the first version: first to select the acceptable values of the parameters and a second time for the average distance. Which makes it biased downwards. The second version is more computationally demanding, especially when deriving the associated p-value. It however produces a higher power under the alternative. Obviously depending on how the alternative is defined, since goodness-of-fit is only related to the null, i.e., to a specific model.

From a general perspective, I do not completely agree with the conclusions of the paper in that (a) this is a frequentist assessment and partakes in the shortcomings of p-values and (b) the choice of summary statistics has a huge impact on the decision about the fit since hardly varying statistics are more likely to lead to a good fit than appropriately varying ones.

a unified treatment of predictive model comparison

“Applying various approximation strategies to the relative predictive performance derived from predictive distributions in frequentist and Bayesian inference yields many of the model comparison techniques ubiquitous in practice, from predictive log loss cross validation to the Bayesian evidence and Bayesian information criteria.”

Michael Betancourt (Warwick) just arXived a paper formalising predictive model comparison in an almost Bourbakian sense! Meaning that he adopts therein a very general representation of the issue, with minimal assumptions on the data generating process (excluding a specific metric and obviously the choice of a testing statistic). He opts for an M-open perspective, meaning that this generating process stands outside the hypothetical statistical model or, in Lindley’s terms, a small world. Within this paradigm, the only way to assess the fit of a model seems to be through the predictive performances of that model. Using for instance an f-divergence like the Kullback-Leibler divergence, based on the true generated process as the reference. I think this however puts a restriction on the choice of small worlds as the probability measure on that small world has to be absolutely continuous wrt the true data generating process for the distance to be finite. While there are arguments in favour of absolutely continuous small worlds, this assumes a knowledge about the true process that we simply cannot gather. Ignoring this difficulty, a relative Kullback-Leibler divergence can be defined in terms of an almost arbitrary reference measure. But as it still relies on the true measure, its evaluation proceeds via cross-validation “tricks” like jackknife and bootstrap. However, on the Bayesian side, using the prior predictive links the Kullback-Leibler divergence with the marginal likelihood. And Michael argues further that the posterior predictive can be seen as the unifying tool behind information criteria like DIC and WAIC (widely applicable information criterion). Which does not convince me towards the utility of those criteria as model selection tools, as there is too much freedom in the way approximations are used and a potential for using the data several times.

Posterior predictive p-values and the convex order

Patrick Rubin-Delanchy and Daniel Lawson [of Warhammer fame!] recently arXived a paper we had discussed with Patrick when he visited Andrew and I last summer in Paris. The topic is the evaluation of the posterior predictive probability of a larger discrepancy between data and model

which acts like a Bayesian p-value of sorts. I discussed several times the reservations I have about this notion on this blog… Including running one experiment on the uniformity of the ppp while in Duke last year. One item of those reservations being that it evaluates the posterior probability of an event that does not exist a priori. Which is somewhat connected to the issue of using the data “twice”.

“A posterior predictive p-value has a transparent Bayesian interpretation.”

Another item that was suggested [to me] in the current paper is the difficulty in defining the posterior predictive (pp), for instance by including latent variables

which reminds me of the multiple possible avatars of the BIC criterion. The question addressed by Rubin-Delanchy and Lawson is how far from the uniform distribution stands this pp when the model is correct. The main result of their paper is that any sub-uniform distribution can be expressed as a particular posterior predictive. The authors also exhibit the distribution that achieves the bound produced by Xiao-Li Meng, Namely that

where P is the above (top) probability. (Hence it is uniform up to a factor 2!) Obviously, the proximity with the upper bound only occurs in a limited number of cases that do not validate the overall use of the ppp. But this is certainly a nice piece of theoretical work.