Archive for Bayesian hypothesis testing

practical Bayesian inference [book review]

Posted in Books, Kids, R, Statistics, University life with tags , , , , , , , , , on April 26, 2018 by xi'an

[Disclaimer: I received this book of Coryn Bailer-Jones for a review in the International Statistical Review and intend to submit a revised version of this post as my review. As usual, book reviews on the ‘Og are reflecting my own definitely personal and highly subjective views on the topic!]

It is always a bit of a challenge to review introductory textbooks as, on the one hand, they are rarely written at the level and with the focus one would personally choose to write them. And, on the other hand, it is all too easy to find issues with the material presented and the way it is presented… So be warned and proceed cautiously! In the current case, Practical Bayesian Inference tries to embrace too much, methinks, by starting from basic probability notions (that should not be unknown to physical scientists, I believe, and which would avoid introducing a flat measure as a uniform distribution over the real line!, p.20). All the way to running MCMC for parameter estimation, to compare models by Bayesian evidence, and to cover non-parametric regression and bootstrap resampling. For instance, priors only make their apparition on page 71. With a puzzling choice of an improper prior (?) leading to an improper posterior (??), which is certainly not the smoothest entry on the topic. “Improper posteriors are a bad thing“, indeed! And using truncation to turn them into proper distributions is not a clear improvement as the truncation point will significantly impact the inference. Discussing about the choice of priors from the beginning has some appeal, but it may also create confusion in the novice reader (although one never knows!). Even asking about “what is a good prior?” (p.73) is not necessarily the best (and my recommended) approach to a proper understanding of the Bayesian paradigm. And arguing about the unicity of the prior (p.119) clashes with my own view of the prior being primarily a reference measure rather than an ideal summary of the available information. (The book argues at some point that there is no fixed model parameter, another and connected source of disagreement.) There is a section on assigning priors (p.113), but it only covers the case of a possibly biased coin without much realism. A feature common to many Bayesian textbooks though. To return to the issue of improper priors (and posteriors), the book includes several warnings about the danger of hitting an undefined posterior (still called a distribution), without providing real guidance on checking for its definition. (A tough question, to be sure.)

“One big drawback of the Metropolis algorithm is that it uses a fixed step size, the magnitude of which can hardly be determined in advance…”(p.165)

When introducing computational techniques, quadratic (or Laplace) approximation of the likelihood is mingled with kernel estimators, which does not seem appropriate. Proposing to check convergence and calibrate MCMC via ACF graphs is helpful in low dimensions, but not in larger dimensions. And while warning about the dangers of forgetting the Jacobians in the Metropolis-Hastings acceptance probability when using a transform like η=ln θ is well-taken, the loose handling of changes of variables may be more confusing than helpful (p.167). Discussing and providing two R codes for the (standard) Metropolis algorithm may prove too much. Or not. But using a four page R code for fitting a simple linear regression with a flat prior (pp.182-186) may definitely put the reader off! Even though I deem the example a proper experiment in setting a Metropolis algorithm and appreciate the detailed description around the R code itself. (I just take exception at the paragraph on running the code with two or even one observation, as the fact that “the Bayesian solution always exists” (p.188) [under a proper prior] is not necessarily convincing…)

“In the real world we cannot falsify a hypothesis or model any more than we “truthify” it (…) All we can do is ask which of the available models explains the data best.” (p.224)

In a similar format, the discussion on testing of hypotheses starts with a lengthy presentation of classical tests and p-values, the chapter ending up with a list of issues. Most of them reasonable in my own referential. I also concur with the conclusive remarks quoted above that what matters is a comparison of (all relatively false) models. What I less agree [as predictable from earlier posts and papers] with is the (standard) notion that comparing two models with a Bayes factor follows from the no information (in order to avoid the heavily loaded non-informative) prior weights of ½ and ½. Or similarly that the evidence is uniquely calibrated. Or, again, using a truncated improper prior under one of the assumptions (with the ghost of the Jeffreys-Lindley paradox lurking nearby…).  While the Savage-Dickey approximation is mentioned, the first numerical resolution of the approximation to the Bayes factor is via simulations from the priors. Which may be very poor in the situation of vague and uninformative priors. And then the deadly harmonic mean makes an entry (p.242), along with nested sampling… There is also a list of issues about Bayesian model comparison, including (strong) dependence on the prior, dependence on irrelevant alternatives, lack of goodness of fit tests, computational costs, including calls to possibly intractable likelihood function, ABC being then mentioned as a solution (which it is not, mostly).

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Can we have our Bayesian cake and eat it too?

Posted in Books, pictures, Statistics, University life with tags , , , , , , on January 17, 2018 by xi'an

This paper aims at solving the Bartlett-Lindley-Jeffreys paradox, i.e., the difficulty connected with improper priors in Bayes factors. The introduction is rather lengthy since by page 9 we are still (dis-)covering the Lindley paradox, along with the introduction of a special notation for -2 times the logarithm of the Bayes factor.

“We will now resolve Lindley’s paradox in both of the above examples.”

The “resolution” of the paradox stands in stating the well-known consistency of the Bayes factor, i.e., that as the sample grows to infinity it goes to infinity (almost surely) under the null hypothesis and to zero under the alternative (almost surely again, both statements being for fixed parameters.) Hence the discrepancy between a small p-value and a Bayes factor favouring the null occurs “with vanishingly small” probability. (The authors distinguish between Bartlett’s paradox associated with a prior variance going to infinity [or a prior becoming improper] and Lindley-Jeffreys’ paradox associated with a sample size going to infinity.)

“We construct cake priors using the following ingredients”

The “cake” priors are defined as pseudo-normal distributions, pseudo in the sense that they look like multivariate Normal densities, except for the covariance matrix that also depends on the parameter, as e.g. in the Fisher information matrix. This reminds me of a recent paper of Ronald Gallant in the Journal of Financial Econometrics that I discussed. With the same feature. Except for a scale factor inversely log-proportional to the dimension of the model. Now, what I find most surprising, besides the lack of parameterisation invariance, is that these priors are not normalised. They do no integrate to one. As to whether or not they integrate, the paper keeps silent about this. This is also a criticism I addressed to Gallant’s paper, getting no satisfactory answer. This is a fundamental shortcoming of the proposed cake priors…

“Hence, the relative rates that g⁰ and g¹ diverge must be considered”

The authors further argue (p.12) that by pushing the scale factors to infinity one produces the answer the Jeffreys prior would have produced. This is not correct since the way the scale factors diverge, relative to one another, drives the numerical value of the limit! Using inversely log-proportionality in the dimension(s) of the model(s) is a correct solution, from a mathematical perspective. But only from a mathematical perspective.

“…comparing the LRT and Bayesian tests…”

Since the log-Bayes factor is the log-likelihood ratio modulo the ν log(n) BIC correction, it is not very surprising that both approaches reach close answers when the scale goes to infinity and the sample size n as well. In the end, there seems to be no reason for going that path other than making likelihood ratio and Bayes factor asymptotically coincide, which does not sound like a useful goal to me. (And so does recovering BIC in the linear model.)

“No papers in the model selection literature, to our knowledge, chose different constants for each model under consideration.”

In conclusion, the paper sets up a principled or universal way to cho<a href=”https://academic.oup.com/jfec/article-abstract/14/2/265/1751312?redirectedFrom=fulltext”></a><a href=”https://xiaose “cake” priors fighting Lindley-Jeffreys’ paradox, but the choices made therein remain arbitrary. They allow for a particular limit to be found when the scale parameter(s) get to infinity, but the limit depends on the connection created between the models, which should not share parameters if one is to be chosen. (The discussion of using improper priors and arbitrary constants is aborted, resorting to custom arguments as the above.) The paper thus unfortunately does not resolve Lindley-Jeffreys’ paradox and the vexing issue of improper priors unfit for testing.

abandon all o(p) ye who enter here

Posted in Books, Statistics, University life with tags , , , , , , on September 28, 2017 by xi'an

Today appeared on arXiv   a joint paper by Blakeley McShane, David Gal, Andrew Gelman, Jennifer Tackett, and myself, towards the abandonment of significance tests, which is a response to the 72 author paper in Nature Methods that recently made the news (and comments on the ‘Og). Some of these comments have been incorporated in the paper, along with others more on the psychology testing side. From the irrelevance of point null hypotheses to the numerous incentives for multiple comparisons, to the lack of sufficiency of the p-value itself, to the limited applicability of the uniformly most powerful prior principle…

“…each [proposal] is a purely statistical measure that fails to take a more holistic view of the evidence that includes the consideration of the traditionally neglected factors, that is, prior and related evidence, plausibility of mechanism, study design and data quality, real world costs and benefits, novelty of finding, and other factors that vary by research domain.”

One may wonder about this list of grievances and its impact on statistical practice. The paper however suggests two alternatives, one being to investigate the potential impact of (neglected) factors rather than relying on thresholds. Another one, maybe less realistic, unless it is the very same, is to report the entirety of the data associated with the experiment. This makes the life of journal editors and grant evaluators harder, possibly much harder, but it indeed suggests an holistic and continuous approach to data analysis, rather than the mascarade of binary outputs. (Not surprisingly, posting this item of news on Andrew’s blog a few hours ago generated a large amount of discussion.)

A Milano [not jatp]

Posted in Kids, Mountains, pictures, Statistics, Travel, University life, Wines with tags , , , , , , , , on October 7, 2016 by xi'an

Today, I went to Milano for 13 hours to give a seminar at l’Università Bocconi. Where I thus gave a talk on Testing via mixtures (using the same slides as at ISBA last Spring). It was the first time I was in Milano (and thus at Bocconi) for more than a transfer to MCMski or to Pavia and it was great to walk through the city. And of course to meet and share with many friends there. While I glimpsed the end of the sunrise on the Italian Alps (near Monte Rosa?!), I was too late on my way back for the sunset.

contemporary issues in hypothesis testing

Posted in Statistics with tags , , , , , , , , , , , , , , , , , , on September 26, 2016 by xi'an

hipocontemptThis week [at Warwick], among other things, I attended the CRiSM workshop on hypothesis testing, giving the same talk as at ISBA last June. There was a most interesting and unusual talk by Nick Chater (from Warwick) about the psychological aspects of hypothesis testing, namely about the unnatural features of an hypothesis in everyday life, i.e., how far this formalism stands from human psychological functioning.  Or what we know about it. And then my Warwick colleague Tom Nichols explained how his recent work on permutation tests for fMRIs, published in PNAS, testing hypotheses on what should be null if real data and getting a high rate of false positives, got the medical imaging community all up in arms due to over-simplified reports in the media questioning the validity of 15 years of research on fMRI and the related 40,000 papers! For instance, some of the headings questioned the entire research in the area. Or transformed a software bug missing the boundary effects into a major flaw.  (See this podcast on Not So Standard Deviations for a thoughtful discussion on the issue.) One conclusion of this story is to be wary of assertions when submitting a hot story to journals with a substantial non-scientific readership! The afternoon talks were equally exciting, with Andrew explaining to us live from New York why he hates hypothesis testing and prefers model building. With the birthday model as an example. And David Draper gave an encompassing talk about the distinctions between inference and decision, proposing a Jaynes information criterion and illustrating it on Mendel‘s historical [and massaged!] pea dataset. The next morning, Jim Berger gave an overview on the frequentist properties of the Bayes factor, with in particular a novel [to me] upper bound on the Bayes factor associated with a p-value (Sellke, Bayarri and Berger, 2001)

B¹⁰(p) ≤ 1/-e p log p

with the specificity that B¹⁰(p) is not testing the original hypothesis [problem] but a substitute where the null is the hypothesis that p is uniformly distributed, versus a non-parametric alternative that p is more concentrated near zero. This reminded me of our PNAS paper on the impact of summary statistics upon Bayes factors. And of some forgotten reference studying Bayesian inference based solely on the p-value… It is too bad I had to rush back to Paris, as this made me miss the last talks of this fantastic workshop centred on maybe the most important aspect of statistics!

non-local priors for mixtures

Posted in Statistics, University life with tags , , , , , , , , , , , , , , , on September 15, 2016 by xi'an

[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 foFaith, Barossa Valley wine: strange name for a Shiraz (as it cannot be a mass wine!, but nice flavoursr 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.

reversible chain[saw] massacre

Posted in Books, pictures, R, Statistics, University life with tags , , , , , , , , on May 16, 2016 by xi'an

A paper in Nature this week that uses reversible-jump MCMC, phylogenetic trees, and Bayes factors. And that looks at institutionalised or ritual murders in Austronesian cultures. How better can it get?!

“by applying Bayesian phylogenetic methods (…) we find strong support for models in which human sacrifice stabilizes social stratification once stratification has arisen, and promotes a shift to strictly inherited class systems.” Joseph Watts et al.

The aim of the paper is to establish that societies with human sacrifices are more likely to have become stratified and stable than societies without such niceties. The hypothesis to be tested is then about the evolution towards more stratified societies rather the existence of a high level of stratification.

“The social control hypothesis predicts that human sacrifice (i) co-evolves with social stratification, (ii) increases the chance of a culture gaining social stratification, and (iii) reduces the chance of a culture losing social stratification once stratification has arisen.” Joseph Watts et al.

The methodological question is then how can this be tested when considering those are extinct societies about which little is known. Grouping together moderate and high stratification societies against egalitarian societies, the authors tested independence of both traits versus dependence, with a resulting Bayes factor of 3.78 in favour of the latest. Other hypotheses of a similar flavour led to Bayes factors in the same range. Which is thus not overwhelming. Actually, given that the models are quite simplistic, I do not agree that those Bayes factors prove anything of the magnitude of such anthropological conjectures. Even if the presence/absence of human sacrifices is confirmed in all of the 93 societies, and if the stratification of the cultures is free from uncertainties, the evolutionary part is rather involved, from my neophyte point of view: the evolutionary structure (reproduced above) is based on a sample of 4,200 trees based on Bayesian analysis of Austronesian basic vocabulary items, followed by a call to the BayesTrait software to infer about evolution patterns between stratification levels, concluding (with p-values!) at a phylogenetic structure of the data. BayesTrait was also instrumental in deriving MLEs for the various transition rates, “in order to inform our choice of priors” (!). BayesTrait has an MCMC function used by the authors “to test for correlated evolution between traits” and derive the above Bayes factors. Using a stepping-stone method I am unaware of. And 10⁹ iterations (repeated 3 times for checking consistency)… Reversible jump is apparently used to move between constrained and unconstrained models, leading to the pie charts at the inner nodes of the above picture. Again a by-product of BayesTrait. The trees on the left and the right are completely identical, the difference being in the inference about stratification evolution (right) and sacrifice evolution (left). While the overall hypothesis makes sense at my layman level (as a culture has to be stratified enough to impose sacrifices from its members), I am not convinced that this involved statistical analysis brings that strong a support. (But it would make a fantastic topic for an undergraduate or a Master thesis!)