non-local priors for mixtures

[For some unknown reason, this commentary on the paper by Jairo Fúquene, Mark Steel, David Rossell —all colleagues at Warwick— on choosing mixture components by non-local priors remained untouched in my draft box…]

Choosing the number of components in a mixture of (e.g., Gaussian) distributions is a hard problem. It may actually be an altogether impossible problem, even when abstaining from moral judgements on mixtures. I do realise that the components can eventually be identified as the number of observations grows to infinity, as demonstrated for instance by Judith Rousseau and Kerrie Mengersen (2011). But for a finite and given number of observations, how much can we trust any conclusion about the number of components?! It seems to me that the criticism about the vacuity of point null hypotheses, namely the logical absurdity of trying to differentiate θ=0 from any other value of θ, applies to the estimation or test on the number of components of a mixture. Doubly so, one might argue, since a very small or a very close component is undistinguishable from a non-existing one. For instance, Definition 2 is correct from a mathematical viewpoint, but it does not spell out the multiple contiguities between k and k’ component mixtures.

The paper starts with a comprehensive coverage of l’état de l’art… When using a Bayes factor to compare a k-component and an h-component mixture, the behaviour of the factor is quite different depending on which model is correct. Essentially overfitted mixtures take much longer to detect than underfitted ones, which makes intuitive sense. And BIC should be corrected for overfitted mixtures by a canonical dimension λ between the true and the (larger) assumed number of parameters  into

2 log m(y) = 2 log p(y|θ) – λ log O(n) + O(log log n)

I would argue that this purely invalidates BIG in mixture settings since the canonical dimension λ is unavailable (and DIC does not provide a useful substitute as we illustrated a decade ago…) The criticism about Rousseau and Mengersen (2011) over-fitted mixture that their approach shrinks less than a model averaging over several numbers of components relates to minimaxity and hence sounds both overly technical and reverting to some frequentist approach to testing. Replacing testing with estimating sounds like the right idea.  And I am also unconvinced that a faster rate of convergence of the posterior probability or of the Bayes factor is a relevant factor when conducting

As for non local priors, the notion seems to rely on a specific topology for the parameter space since a k-component mixture can approach a k’-component mixture (when k'<k) in a continuum of ways (even for a given parameterisation). This topology seems to be summarised by the penalty (distance?) d(θ) in the paper. Is there an intrinsic version of d(θ), given the weird parameter space? Like one derived from the Kullback-Leibler distance between the models? The choice of how zero is approached clearly has an impact on how easily the “null” is detected, the more because of the somewhat discontinuous nature of the parameter space. Incidentally, I find it curious that only the distance between means is penalised… The prior also assumes independence between component parameters and component weights, which I think is suboptimal in dealing with mixtures, maybe suboptimal in a poetic sense!, as we discussed in our reparameterisation paper. I am not sure either than the speed the distance converges to zero (in Theorem 1) helps me to understand whether the mixture has too many components for the data’s own good when I can run a calibration experiment under both assumptions.

While I appreciate the derivation of a closed form non-local prior, I wonder at the importance of the result. Is it because this leads to an easier derivation of the posterior probability? I do not see the connection in Section 3, except maybe that the importance weight indeed involves this normalising constant when considering several k’s in parallel. Is there any convergence issue in the importance sampling solution of (3.1) and (3.3) since the simulations are run under the local posterior? While I appreciate the availability of an EM version for deriving the MAP, a fact I became aware of only recently, is it truly bringing an improvement when compared with picking the MCMC simulation with the highest completed posterior?

The section on prior elicitation is obviously of central interest to me! It however seems to be restricted to the derivation of the scale factor g, in the distance, and of the parameter q in the Dirichlet prior on the weights. While the other parameters suffer from being allocated the conjugate-like priors. I would obviously enjoy seeing how this approach proceeds with our non-informative prior(s). In this regard, the illustration section is nice, but one always wonders at the representative nature of the examples and the possible interpretations of real datasets. For instance, when considering that the Old Faithful is more of an HMM than a mixture.

Dirichlet process mixture inconsistency

Judith Rousseau pointed out to me this NIPS paper by Jeff Miller and Matthew Harrison on the possible inconsistency of Dirichlet mixtures priors for estimating the (true) number of components in a (true) mixture model. The resulting posterior on the number of components does not concentrate on the right number of components. Which is not the case when setting a prior on the unknown number of components of a mixture, where consistency occurs. (The inconsistency results established in the paper are actually focussed on iid Gaussian observations, for which the estimated number of Gaussian components is almost never equal to 1.) In a more recent arXiv paper, they also show that a Dirichlet prior on the weights and a prior on the number of components can still produce the same features as a Dirichlet mixtures priors. Even the stick breaking representation! (Paper that I already reviewed last Spring.)

mixtures of mixtures

And yet another arXival of a paper on mixtures! This one is written by Gertraud Malsiner-Walli, Sylvia Frühwirth-Schnatter, and Bettina Grün, from the Johannes Kepler University Linz and the Wirtschaftsuniversitat Wien I visited last September. With the exact title being Identifying mixtures of mixtures using Bayesian estimation.

So, what is a mixture of mixtures if not a mixture?! Or if not only a mixture. The upper mixture level is associated with clusters, while the lower mixture level is used for modelling the distribution of a given cluster. Because the cluster needs to be real enough, the components of the mixture are assumed to be heavily overlapping. The paper thus spends a large amount of space on detailing the construction of the associated hierarchical prior. Which in particular implies defining through the prior what a cluster means. The paper also connects with the overfitting mixture idea of Rousseau and Mengersen (2011, Series B). At the cluster level, the Dirichlet hyperparameter is chosen to be very small, 0.001, which empties superfluous clusters but sounds rather arbitrary (which is the reason why we did not go for such small values in our testing/mixture modelling). On the opposite, the mixture weights have an hyperparameter staying (far) away from zero. The MCMC implementation is based on a standard Gibbs sampler and the outcome is analysed and sorted by estimating the “true” number of clusters as the MAP and by selecting MCMC simulations conditional on that value. From there clusters are identified via the point process representation of a mixture posterior. Using a standard k-means algorithm.

The remainder of the paper illustrates the approach on simulated and real datasets. Recovering in those small dimension setups the number of clusters used in the simulation or found in other studies. As noted in the conclusion, using solely a Gibbs sampler with such a large number of components is rather perilous since it may get stuck close to suboptimal configurations. Especially with very small Dirichlet hyperparameters.

Harold Jeffreys’ default Bayes factor [for psychologists]

“One of Jeffreys’ goals was to create default Bayes factors by using prior distributions that obeyed a series of general desiderata.”

The paper Harold Jeffreys’s default Bayes factor hypothesis tests: explanation, extension, and application in Psychology by Alexander Ly, Josine Verhagen, and Eric-Jan Wagenmakers is both a survey and a reinterpretation cum explanation of Harold Jeffreys‘ views on testing. At about the same time, I received a copy from Alexander and a copy from the journal it had been submitted to! This work starts with a short historical entry on Jeffreys’ work and career, which includes four of his principles, quoted verbatim from the paper:

1. “scientific progress depends primarily on induction”;
2. “in order to formalize induction one requires a logic of partial belief” [enters the Bayesian paradigm];
3. “scientific hypotheses can be assigned prior plausibility in accordance with their complexity” [a.k.a., Occam’s razor];
4. “classical “Fisherian” p-values are inadequate for the purpose of hypothesis testing”.

“The choice of π(σ)  therefore irrelevant for the Bayes factor as long as we use the same weighting function in both models”

A very relevant point made by the authors is that Jeffreys only considered embedded or nested hypotheses, a fact that allows for having common parameters between models and hence some form of reference prior. Even though (a) I dislike the notion of “common” parameters and (b) I do not think it is entirely legit (I was going to write proper!) from a mathematical viewpoint to use the same (improper) prior on both sides, as discussed in our Statistical Science paper. And in our most recent alternative proposal. The most delicate issue however is to derive a reference prior on the parameter of interest, which is fixed under the null and unknown under the alternative. Hence preventing the use of improper priors. Jeffreys tried to calibrate the corresponding prior by imposing asymptotic consistency under the alternative. And exact indeterminacy under “completely uninformative” data. Unfortunately, this is not a well-defined notion. In the normal example, the authors recall and follow the proposal of Jeffreys to use an improper prior π(σ)∝1/σ on the nuisance parameter and argue in his defence the quote above. I find this argument quite weak because suddenly the prior on σ becomes a weighting function... A notion foreign to the Bayesian cosmology. If we use an improper prior for π(σ), the marginal likelihood on the data is no longer a probability density and I do not buy the argument that one should use the same measure with the same constant both on σ alone [for the nested hypothesis] and on the σ part of (μ,σ) [for the nesting hypothesis]. We are considering two spaces with different dimensions and hence orthogonal measures. This quote thus sounds more like wishful thinking than like a justification. Similarly, the assumption of independence between δ=μ/σ and σ does not make sense for σ-finite measures. Note that the authors later point out that (a) the posterior on σ varies between models despite using the same data [which shows that the parameter σ is far from common to both models!] and (b) the [testing] Cauchy prior on δ is only useful for the testing part and should be replaced with another [estimation] prior when the model has been selected. Which may end up as a backfiring argument about this default choice.

“Each updated weighting function should be interpreted as a posterior in estimating σ within their own context, the model.”

The re-derivation of Jeffreys’ conclusion that a Cauchy prior should be used on δ=μ/σ makes it clear that this choice only proceeds from an imperative of fat tails in the prior, without solving the calibration of the Cauchy scale. (Given the now-available modern computing tools, it would be nice to see the impact of this scale γ on the numerical value of the Bayes factor.) And maybe it also proceeds from a “hidden agenda” to achieve a Bayes factor that solely depends on the t statistic. Although this does not sound like a compelling reason to me, since the t statistic is not sufficient in this setting.

In a differently interesting way, the authors mention the Savage-Dickey ratio (p.16) as a way to represent the Bayes factor for nested models, without necessarily perceiving the mathematical difficulty with this ratio that we pointed out a few years ago. For instance, in the psychology example processed in the paper, the test is between δ=0 and δ≥0; however, if I set π(δ=0)=0 under the alternative prior, which should not matter [from a measure-theoretic perspective where the density is uniquely defined almost everywhere], the Savage-Dickey representation of the Bayes factor returns zero, instead of 9.18!

“In general, the fact that different priors result in different Bayes factors should not come as a surprise.”

The second example detailed in the paper is the test for a zero Gaussian correlation. This is a sort of “ideal case” in that the parameter of interest is between -1 and 1, hence makes the choice of a uniform U(-1,1) easy or easier to argue. Furthermore, the setting is also “ideal” in that the Bayes factor simplifies down into a marginal over the sample correlation only, under the usual Jeffreys priors on means and variances. So we have a second case where the frequentist statistic behind the frequentist test[ing procedure] is also the single (and insufficient) part of the data used in the Bayesian test[ing procedure]. Once again, we are in a setting where Bayesian and frequentist answers are in one-to-one correspondence (at least for a fixed sample size). And where the Bayes factor allows for a closed form through hypergeometric functions. Even in the one-sided case. (This is a result obtained by the authors, not by Jeffreys who, as the proper physicist he was, obtained approximations that are remarkably accurate!)

“The fact that the Bayes factor is independent of the intention with which the data have been collected is of considerable practical importance.”

The authors have a side argument in this section in favour of the Bayes factor against the p-value, namely that the “Bayes factor does not depend on the sampling plan” (p.29), but I find this fairly weak (or tongue in cheek) as the Bayes factor does depend on the sampling distribution imposed on top of the data. It appears that the argument is mostly used to defend sequential testing.

“The Bayes factor (…) balances the tension between parsimony and goodness of fit, (…) against overfitting the data.”

In fine, I liked very much this re-reading of Jeffreys’ approach to testing, maybe the more because I now think we should get away from it! I am not certain it will help in convincing psychologists to adopt Bayes factors for assessing their experiments as it may instead frighten them away. And it does not bring an answer to the vexing issue of the relevance of point null hypotheses. But it constitutes a lucid and innovative of the major advance represented by Jeffreys’ formalisation of Bayesian testing.