## read paper [in Bristol]

Posted in Books, pictures, Statistics, Travel, University life with tags , , , , , , , , , , , , , , on January 29, 2016 by xi'an

I went to give a seminar in Bristol last Friday and I chose to present the testing with mixture paper. As we are busy working on the revision, I was eagerly looking for comments and criticisms that could strengthen this new version. As it happened, the (Bristol) Bayesian Cake (Reading) Club had chosen our paper for discussion, two weeks in a row!, hence the title!, and I got invited to join the group the morning prior to the seminar! This was, of course, most enjoyable and relaxed, including an home-made cake!, but also quite helpful in assessing our arguments in the paper. One point of contention or at least of discussion was the common parametrisation between the components of the mixture. Although all parametrisations are equivalent from a single component point of view, I can [almost] see why using a mixture with the same parameter value on all components may impose some unsuspected constraint on that parameter. Even when the parameter is the same moment for both components. This still sounds like a minor counterpoint in that the weight should converge to either zero or one and hence eventually favour the posterior on the parameter corresponding to the “true” model.

Another point that was raised during the discussion is the behaviour of the method under misspecification or for an M-open framework: when neither model is correct does the weight still converge to the boundary associated with the closest model (as I believe) or does a convexity argument produce a non-zero weight as it limit (as hinted by one example in the paper)? I had thought very little about this and hence had just as little to argue though as this does not sound to me like the primary reason for conducting tests. Especially in a Bayesian framework. If one is uncertain about both models to be compared, one should have an alternative at the ready! Or use a non-parametric version, which is a direction we need to explore deeper before deciding it is coherent and convergent!

A third point of discussion was my argument that mixtures allow us to rely on the same parameter and hence the same prior, whether proper or not, while Bayes factors are less clearly open to this interpretation. This was not uniformly accepted!

Thinking afresh about this approach also led me to broaden my perspective on the use of the posterior distribution of the weight(s) α: while previously I had taken those weights mostly as a proxy to the posterior probabilities, to be calibrated by pseudo-data experiments, as for instance in Figure 9, I now perceive them primarily as the portion of the data in agreement with the corresponding model [or hypothesis] and more importantly as a solution for staying away from a Neyman-Pearson-like decision. Or error evaluation. Usually, when asked about the interpretation of the output, my answer is to compare the behaviour of the posterior on the weight(s) with a posterior associated with a sample from each model. Which does sound somewhat similar to posterior predictives if the samples are simulated from the associated predictives. But the issue was not raised during the visit to Bristol, which possibly reflects on how unfrequentist the audience was [the Statistics group is], as it apparently accepted with no further ado the use of a posterior distribution as a soft assessment of the comparative fits of the different models. If not necessarily agreeing the need of conducting hypothesis testing (especially in the case of the Pima Indian dataset!).

## on the origin of the Bayes factor

Posted in Books, Statistics with tags , , , , , , , on November 27, 2015 by xi'an

Alexander Etz and Eric-Jan Wagenmakers from the Department of Psychology of the University of Amsterdam just arXived a paper on the invention of the Bayes factor. In particular, they highlight the role of John Burdon Sanderson (J.B.S.) Haldane in the use of the central tool for Bayesian comparison of hypotheses. In short, Haldane used a Bayes factor before Jeffreys did!

“The idea of a significance test, I suppose, putting half the probability into a constant being 0, and distributing the other half over a range of possible values.”H. Jeffreys

The authors analyse Jeffreys’ 1935 paper on significance tests, which appears to be the very first occurrence of a Bayes factor in his bibliography, testing whether or not two probabilities are equal. They also show the roots of this derivation in earlier papers by Dorothy Wrinch and Harold Jeffreys. [As an “aside”, the early contributions of Dorothy Wrinch to the foundations of 20th Century Bayesian statistics are hardly acknowledged. A shame, when considering they constitute the basis and more of Jeffreys’ 1931 Scientific Inference, Jeffreys who wrote in her necrology “I should like to put on record my appreciation of the substantial contribution she made to [our joint] work, which is the basis of all my later work on scientific inference.” In retrospect, Dorothy Wrinch should have been co-author to this book…] As early as 1919. These early papers by Wrinch and Jeffreys are foundational in that they elaborate a construction of prior distributions that will eventually see the Jeffreys non-informative prior as its final solution [Jeffreys priors that should be called Lhostes priors according to Steve Fienberg, although I think Ernest Lhoste only considered a limited number of transformations in his invariance rule]. The 1921 paper contains de facto the Bayes factor but it does not appear to be advocated as a tool per se for conducting significance tests.

“The historical records suggest that Haldane calculated the first Bayes factor, perhaps almost by accident, before Jeffreys did.” A. Etz and E.J. Wagenmakers

As another interesting aside, the historical account points out that Jeffreys came out in 1931 with what is now called Haldane’s prior for a Binomial proportion, proposed in 1931 (when the paper was read) and in 1932 (when the paper was published in the Mathematical Proceedings of the Cambridge Philosophical Society) by Haldane. The problem tackled by Haldane is again a significance on a Binomial probability. Contrary to the authors, I find the original (quoted) text quite clear, with a prior split before a uniform on [0,½] and a point mass at ½. Haldane uses a posterior odd [of 34.7] to compare both hypotheses but… I see no trace in the quoted material that he ends up using the Bayes factor as such, that is as his decision rule. (I acknowledge decision rule is anachronistic in this setting.) On the side, Haldane also implements model averaging. Hence my reading of this reading of the 1930’s literature is that it remains unclear that Haldane perceived the Bayes factor as a Bayesian [another anachronism] inference tool, upon which [and only which] significance tests could be conducted. That Haldane had a remarkably modern view of splitting the prior according to two orthogonal measures and of correctly deriving the posterior odds is quite clear. With the very neat trick of removing the infinite integral at p=0, an issue that Jeffreys was fighting with at the same time. In conclusion, I would thus rephrase the major finding of this paper as Haldane should get the priority in deriving the Bayesian significance test for point null hypotheses, rather than in deriving the Bayes factor. But this may be my biased views of Bayes factors speaking there…

Another amazing fact I gathered from the historical work of Etz and Wagenmakers is that Haldane and Jeffreys were geographically very close while working on the same problem and hence should have known and referenced their respective works. Which did not happen.

## O’Bayes 2015 [day #3]

Posted in Statistics, Travel, University life, Wines with tags , , , , , , , , on June 5, 2015 by xi'an

The third day of the meeting was a good illustration of the diversity of the themes [says a member of the scientific committee!], from “traditional” O’Bayes talks on reference priors by the father of all reference priors (!), José Bernardo, re-examinations of expected posterior priors, on properties of Bayes factors, or on new versions of the Lindley-Jeffreys paradox, to the radically different approach of Simpson et al. presented by Håvard Rue. I was obviously most interested in posterior expected priors!, with the new notion brought in by Dimitris Fouskakis, Ioannis Ntzoufras and David Draper of a lower impact of the minimal sample on the resulting prior by the trick of a lower (than one) power of the likelihood. Since this change seemed to go beyond the “minimal” in minimal sample size, I am somehow puzzled that this can be achieved, but the normal example shows this is indeed possible. The next difficulty is then in calibrating this power as I do not see any intuitive justification in a specific power. The central talk of the day was in my opinion Håvard’s as it challenged most tenets of the Objective Bayes approach, presented in a most eager tone, even though it did not generate particularly heated comments from the audience. I have already discussed here an earlier version of this paper and I keep on thinking this proposal for PC priors is a major breakthrough in the way we envision priors and their derivation. I was thus sorry to hear the paper had not been selected as a Read Paper by the Royal Statistical Society, as it would have nicely suited an open discussion, but I hope it will find another outlet that allows for a discussion! As an aside, Håvard discussed the case of a Student’s t degree of freedom as particularly challenging for prior construction, albeit I would have analysed the problem using instead a model choice perspective (on an usually continuous space of models).

As this conference day had a free evening, I took the tram with friends to the town beach and we had a fantastic [if hurried] dinner in a small bodega [away from the uninspiring beach front] called Casa Montaña, a place decorated with huge barrels, offering amazing tapas and wines, a perfect finale to my Spanish trip. Too bad we had to vacate the dinner room for the next batch of customers…

## using mixtures towards Bayes factor approximation

Posted in Statistics, Travel, University life with tags , , , , , , on December 11, 2014 by xi'an

Phil O’Neill and Theodore Kypraios from the University of Nottingham have arXived last week a paper on “Bayesian model choice via mixture distributions with application to epidemics and population process models”. Since we discussed this paper during my visit there earlier this year, I was definitely looking forward the completed version of their work. Especially because there are some superficial similarities with our most recent work on… Bayesian model choice via mixtures! (To the point that I misunderstood at the beginning their proposal for ours…)

The central idea in the paper is that, by considering the mixture likelihood

$\alpha\ell_1(\theta_1|\mathbf{x})+(1-\alpha)\ell_2(\theta_2|\mathbf{x})$

where x corresponds to the entire sample, it is straighforward to relate the moments of α with the Bayes factor, namely

$\mathfrak{B}_{12}=\dfrac{\mathbb{E}[\alpha]-\mathbb{E}[\alpha^2]-\mathbb{E}[\alpha|\mathbf{x}](1-\mathbb{E}[\alpha])}{\mathbb{E}[\alpha]\mathbb{E}[\alpha|\mathbf{x}]-\mathbb{E}[\alpha^2]}$

which means that estimating the mixture weight α by MCMC is equivalent to estimating the Bayes factor.

What puzzled me at first was that the mixture weight is in fine estimated with a single “datapoint”, made of the entire sample. So the posterior distribution on α is hardly different from the prior, since it solely varies by one unit! But I came to realise that this is a numerical tool and that the estimator of α is not meaningful  from a statistical viewpoint (thus differing completely from our perspective). This explains why the Beta prior on α can be freely chosen so that the mixing and stability of the Markov chain is improved: This parameter is solely an algorithmic entity.

There are similarities between this approach and the pseudo-prior encompassing perspective of Carlin and Chib (1995), even though the current version does not require pseudo-priors, using true priors instead. But thinking of weakly informative priors and of the MCMC consequence (see below) leads me to wonder if pseudo-priors would not help in this setting…

Another aspect of the paper that still puzzles me is that the MCMC algorithm mixes at all: indeed, depending on the value of the binary latent variable z, one of the two parameters is updated from the true posterior while the other is updated from the prior. It thus seems unlikely that the value of z would change quickly. Creating a huge imbalance in the prior can counteract this difference, but the same problem occurs once z has moved from 0 to 1 or from 1 to 0. It seems to me that resorting to a common parameter [if possible] and using as a proposal the model-based posteriors for both parameters is the only way out of this conundrum. (We do certainly insist on this common parametrisation in our approach as it is paramount to the use of improper priors.)

“In contrast, we consider the case where there is only one datum.”

The idea in the paper is therefore fully computational and relates to other linkage methods that create bridges between two models. It differs from our new notion of Bayesian testing in that we consider estimating the mixture between the two models in comparison, hence considering instead the mixture

$\prod_{i=1}^n\alpha f_1(x_i|\theta_1)+(1-\alpha) f_2(x_i|\theta_2)$

which is another model altogether and does not recover the original Bayes factor (Bayes factor that we altogether dismiss in favour of the posterior median of α and its entire distribution).

## differences between Bayes factors and normalised maximum likelihood

Posted in Books, Kids, Statistics, University life with tags , , , , on November 19, 2014 by xi'an

A recent arXival by Heck, Wagenmaker and Morey attracted my attention: Three Qualitative Differences Between Bayes Factors and Normalized Maximum Likelihood, as it provides an analysis of the differences between Bayesian analysis and Rissanen’s Optimal Estimation of Parameters that I reviewed a while ago. As detailed in this review, I had difficulties with considering the normalised likelihood

$p(x|\hat\theta_x) \big/ \int_\mathcal{X} p(y|\hat\theta_y)\,\text{d}y$

as the relevant quantity. One reason being that the distribution does not make experimental sense: for instance, how can one simulate from this distribution? [I mean, when considering only the original distribution.] Working with the simple binomial B(n,θ) model, the authors show the quantity corresponding to the posterior probability may be constant for most of the data values, produces a different upper bound and hence a different penalty of model complexity, and may differ in conclusion for some observations. Which means that the apparent proximity to using a Jeffreys prior and Rissanen’s alternative does not go all the way. While it is a short note and only focussed on producing an illustration in the Binomial case, I find it interesting that researchers investigate the Bayesian nature (vs. artifice!) of this approach…

## how to translate evidence into French?

Posted in Books, Statistics, University life with tags , , , , , on July 6, 2014 by xi'an

I got this email from Gauvain who writes a PhD in philosophy of sciences a few minutes ago:

L’auteur du texte que j’ai à traduire désigne les facteurs de Bayes comme une “Bayesian measure of evidence”, et les tests de p-value comme une “frequentist measure of evidence”. Je me demandais s’il existait une traduction française reconnue et établie pour cette expression de “measure of evidence”. J’ai rencontré parfois “mesure d’évidence” qui ressemble fort à un anglicisme, et parfois “estimateur de preuve”, mais qui me semble pouvoir mener à des confusions avec d’autres emploi du terme “estimateur”.

which (pardon my French!) wonders how to translate the term evidence into French. It would sound natural that the French évidence is the answer but this is not the case. Despite sharing the same Latin root (evidentia), since the English version comes from medieval French, the two words have different meanings: in English, it means a collection of facts coming to support an assumption or a theory, while in French it means something obvious, which truth is immediately perceived. Surprisingly, English kept the adjective evident with the same [obvious] meaning as the French évident. But the noun moved towards a much less definitive meaning, both in Law and in Science. I had never thought of the huge gap between the two meanings but must have been surprised at its use the first time I heard it in English. But does not think about it any longer, as when I reviewed Seber’s Evidence and Evolution.

One may wonder at the best possible translation of evidence into French. Even though marginal likelihood (vraisemblance marginale) is just fine for statistical purposes. I would suggest faisceau de présomptions or degré de soutien or yet intensité de soupçon as (lengthy) solutions. Soupçon could work as such, but has a fairly negative ring…

## Adaptive revised standards for statistical evidence [guest post]

Posted in Books, Statistics, University life with tags , , , , , , , on March 25, 2014 by xi'an

[Here is a discussion of Valen Johnson’s PNAS paper written by Luis Pericchi, Carlos Pereira, and María-Eglée Pérez, in conjunction with an arXived paper of them I never came to discuss. This has been accepted by PNAS along with a large number of other letters. Our discussion permuting the terms of the original title also got accepted.]

Johnson [1] argues for decreasing the bar of statistical significance from 0.05 and 0.01 to 0:005 and 0:001 respectively. There is growing evidence that the canonical fixed standards of significance are inappropriate. However, the author simply proposes other fixed standards. The essence of the problem of classical testing of significance lies on its goal of minimizing type II error (false negative) for a fixed type I error (false positive). A real departure instead would be to minimize a weighted sum of the two errors, as proposed by Jeffreys [2]. Significance levels that are constant with respect to sample size do not balance errors. Size levels of 0.005 and 0.001 certainly will lower false positives (type I error) to the expense of increasing type II error, unless the study is carefully de- signed, which is not always the case or not even possible. If the sample size is small the type II error can become unacceptably large. On the other hand for large sample sizes, 0.005 and 0.001 levels may be too high. Consider the Psychokinetic data, Good [3]: the null hypothesis is that individuals can- not change by mental concentration the proportion of 1’s in a sequence of n = 104; 490; 000 0’s and 1’s, generated originally with a proportion of 1=2. The proportion of 1’s recorded was 0:5001768. The observed p-value is p = 0.0003, therefore according to the present revision of standards, still the null hypothesis is rejected and a Psychokinetic effect claimed. This is contrary to intuition and to virtually any Bayes Factor. On the other hand to make the standards adaptable to the amount of information (see also Raftery [4]) Perez and Pericchi [5] approximate the behavior of Bayes Factors by,

$\alpha_{\mathrm{ref}}(n)=\alpha\,\dfrac{\sqrt{n_0(\log(n_0)+\chi^2_\alpha(1))}}{\sqrt{n(\log(n)+\chi^2_\alpha(1))}}$

This formula establishes a bridge between carefully designed tests and the adaptive behavior of Bayesian tests: The value n0 comes from a theoretical design for which a value of both errors has been specified ed, and n is the actual (larger) sample size. In the Psychokinetic data n0 = 44,529 for type I error of 0:01, type II error of 0.05 to detect a difference of 0.01. The αref (104, 490,000) = 0.00017 and the null of no Psychokinetic effect is accepted.

A simple constant recipe is not the solution to the problem. The standard how to judge the evidence should be a function of the amount of information. Johnson’s main message is to toughen the standards and design the experiments accordingly. This is welcomed whenever possible. But it does not balance type I and type II errors: it would be misleading to pass the message—use now standards divided by ten, regardless of neither type II errors nor sample sizes. This would move the problem without solving it.