relativity is the keyword

As I was teaching my introduction to Bayesian Statistics this morning, ending up with the chapter on tests of hypotheses, I found reflecting [out loud] on the relative nature of posterior quantities. Just like when I introduced the role of priors in Bayesian analysis the day before, I stressed the relativity of quantities coming out of the BBB [Big Bayesian Black Box], namely that whatever happens as a Bayesian procedure is to be understood, scaled, and relativised against the prior equivalent, i.e., that the reference measure or gauge is the prior. This is sort of obvious, clearly, but bringing the argument forward from the start avoids all sorts of misunderstanding and disagreement, in that it excludes the claims of absolute and certainty that may come with the production of a posterior distribution. It also removes the endless debate about the determination of the prior, by making each prior a reference on its own. With an additional possibility of calibration by simulation under the assumed model. Or an alternative. Again nothing new there, but I got rather excited by this presentation choice, as it seems to clarify the path to Bayesian modelling and avoid misapprehensions.

Further, the curious case of the Bayes factor (or of the posterior probability) could possibly be resolved most satisfactorily in this framework, as the [dreaded] dependence on the model prior probabilities then becomes a matter of relativity! Those posterior probabilities depend directly and almost linearly on the prior probabilities, but they should not be interpreted in an absolute sense as the ultimate and unique probability of the hypothesis (which anyway does not mean anything in terms of the observed experiment). In other words, this posterior probability does not need to be scaled against a U(0,1) distribution. Or against the p-value if anyone wishes to do so. By the end of the lecture, I was even wondering [not so loudly] whether or not this perspective was allowing for a resolution of the Lindley-Jeffreys paradox, as the resulting number could be set relative to the choice of the [arbitrary] normalising constant.

not an ASA’s statement on p-values

 

This may be a coincidence, but a few days after the ASA statement got published, Yuri Gurevich and Vladimir Vovk arXived a note on the Fundamentals of p-values. Which actually does not contribute to the debate. The paper is written in a Q&A manner. And defines a sort of peculiar logic related with [some] p-values. A second and more general paper is in the making, which may shed more light on the potential appeal of this formalism…

ASA’s statement on p-values [#2]

 

It took a visit on FiveThirtyEight to realise the ASA statement I mentioned yesterday was followed by individual entries from most members of the panel, much more diverse and deeper than the statement itself! Without discussing each and all comments, some points I subscribe to

• it does not make sense to try to replace the p-value and the 5% boundary by something else but of the same nature. This was the main line of our criticism of Valen Johnson’s PNAS paper with Andrew.
• it does not either make sense to try to come up with a hard set answer about whether or not a certain parameter satisfies a certain constraint. A comparison of predictive performances at or around the observed data sounds much more sensible, if less definitive.
• the Bayes factor is often advanced as a viable alternative to the p-value in those comments, but it suffers from difficulties exposed in our recent testing by mixture paper, one being the lack of absolute scale.
• we seem unable to escape the landscape set by Neyman and Pearson when constructing their testing formalism, including the highly unrealistic 0-1 loss function. And the grossly asymmetric opposition between null and alternative hypotheses.
• the behaviour of any procedure of choice should be evaluated under different scenarios, most likely by simulation, including some accounting for misspecified models. Which may require an extra bit of non-parametrics. And we should abstain from considering further than evaluating whether or not the data looks compatible with each of the scenarios. Or how much through the mixture representation.

ASA’s statement on p-values

 

Last night I received an email from the ASA signed by Jessica Utts and Ron Wasserstein with the following sentence

“Widespread use of ‘statistical significance’ (generally interpreted as ‘p

In short, we envision a new era, in which the broad scientific community recognizes what statisticians have been advocating for many years. In this “post p

Is such an era beyond reach? We think not, but we need your help in making sure this opportunity is not lost.”

which is obviously missing important bits. The email was pointing out a free access American Statistician article warning about the misuses and over-interpretations of p-values. Which contains rather basic “principles” that p-values are not probabilities that the null is true, that there is no golden level against which to compare the p-value, that nominal p-values may be far from actual p-values, that they do not provide a measure of evidence per se, &tc. As written in the conclusion, “Nothing in the ASA statement is new”. But, besides calling for caution and the cumulative use of different assessments of evidence, this statement may leave the non-statistician completely nonplussed about how to proceed when testing hypotheses or comparing models. And make the decision of Basic and Applied Social Psychology of rejecting all arguments based on p-values sound sensible.

Incidentally, the article contains the completion of the first sentence [in red below], if not of the second:

“Widespread use of ‘statistical significance’ (generally interpreted as ‘p≤ 0.05”) as a license for making a claim of a scientific finding (or implied truth) leads to considerable distortion of the scientific process.“

 

statistical significance as explained by The Economist

There is a long article in The Economist of this week (also making the front cover), which discusses how and why many published research papers have unreproducible and most often “wrong” results. Nothing immensely new there, esp. if you read Andrew’s blog on a regular basis, but the (anonymous) writer(s) take(s) pains to explain how this related to statistics and in particular statistical testing of hypotheses. The above is an illustration from this introduction to statistical tests (and their interpretation).

“First, the statistics, which if perhaps off-putting are quite crucial.”

It is not the first time I spot a statistics backed article in this journal and so assume it has either journalists with a statistics background or links with (UK?) statisticians. The description of why statistical tests can err is fairly (Type I – Type II) classical. Incidentally, it reports a finding of Ioannidis that when reporting a positive at level 0.05,  the expectation of a false positive rate of one out of 20 is “highly optimistic”. An evaluation opposed to, e.g., Berger and Sellke (1987) who reported a too-early rejection in a large number of cases. More interestingly, the paper stresses that this classical approach ignores “the unlikeliness of the hypothesis being tested”, which I interpret as the prior probability of the hypothesis under test.

“Statisticians have ways to deal with such problems. But most scientists are not statisticians.”

The paper also reports about the lack of power in most studies, report that I find a bit bizarre and even meaningless in its ability to compute an overall power, all across studies and researchers and even fields. Even in a single study, the alternative to “no effect” is composite, hence has a power that depends on the unknown value of the parameter. Seeking a single value for the power requires some prior distribution on the alternative.

“Peer review’s multiple failings would matter less if science’s self-correction mechanism—replication—was in working order.”

The next part of the paper covers the failings of peer review, of which I discussed in the ISBA Bulletin, but it seems to me too easy to blame the ref in failing to spot statistical or experimental errors, when lacking access to the data or to the full experimental methodology and when under pressure to return (for free) a report within a short time window. The best that can be expected is that a referee detects the implausibility of a claim or an obvious methodological or statistical mistake. These are not math papers! And, as pointed out repeatedly, not all referees are statistically numerate….

“Budding scientists must be taught technical skills, including statistics.”

The last part discusses of possible solutions to achieve reproducibility and hence higher confidence in experimental results. Paying for independent replication is the proposed solution but it can obviously only apply to a small margin of all published results. And having control bodies testing at random labs and teams following a major publication seems rather unrealistic, if only for filling the teams of such bodies with able controllers… An interesting if pessimistic debate, in fine. And fit for the International Year of Statistics.

informative hypotheses (book review)

The title of this book Informative Hypotheses somehow put me off from the start: the author, Hebert Hoijtink, seems to distinguish between informative and uninformative (deformative? disinformative?) hypotheses. Namely, something like

H0: μ₁=μ₂=μ₃=μ₄

is “very informative” and unrealistic, and the alternative Ha is completely uninformative, while the “alternative null”

H1: μ_1<μ₂=μ_3<μ₄

is informative. (Hence the < signs on the cover. One of my book reviews idiosyncrasies is to find hidden meaning behind the cover design…) The idea is thus to have the researcher give some input in the construction of the null hypothesis (as if hypothesis tests usually were not about questions that mattered….).

In fact, this distinction put me off so much that I only ended up reading chapters 1 (an introduction), 3 (an introduction [to the Bayesian processing of such hypotheses]) and 10 (on Bayesian foundations of testing informative hypotheses). Hence a very biased review of Informative Hypotheses that follows….

Given an existing (but out of print?) reference like Robertson, Wright and Dykjstra (1988), that I particularly enjoyed when working on isotonic regression in the mid 90’s, I do not see much of an added value in the present book. The important references are mostly centred on works by the author and his co-authors or students (often Unpublished or In Press), which gives me the impression the book was hurriedly gathered from those papers.

“The Bayes factor (…) is default, objective, based on an appropriate quantification of complexity.” (p.197)

The first chapter of Informative Hypotheses is a motivation for the study of those informative hypotheses, with a focus on ANOVA models. There is not much in the chapter that explains what is so special about those ordering (null) hypotheses and why a whole book is required to cover their processing. A noteworthy specificity of the approach, nonetheless, is that point null hypotheses seem to be replaced with “about equality constraints” (p.9), |μ₂-μ₃|<d, where d is specified by the researcher as significant. This chapter also gives illustrations of ordered (or informative) hypotheses in the settings of analysis of covariance (ANCOVA) and regression models, but does not indicate (yet) how to run the tests. The concluding section is about the epistemological focus of the book, quoting Popper, Sober and Carnap, although I do not see much of a support in those quotes.

“Objective means that Bayes factors based on this prior distribution are essentially independent of this prior distribution.” (p.53)

Chapter 3 starts the introduction to Bayesian statistics with the strange idea of calling the likelihood the “density of the data”. It is indeed the probability density of the model evaluated at the data but… it conveys a confusing meaning since it is not a density when plotted against the parameters (as in Figure 1, p. 44, where, incidentally the exact probability model is not specified). The prior distribution is defined as a normal x inverse chi-square distribution on the vector of the means (in the ANOVA model) and the common variance. Due to the classification of the variance as a nuisance parameter, the author can get away with putting an improper prior on this parameter (p.46). The normal prior is chosen to be “neutral”, i.e. to give the same prior weight to the null and the alternative hypotheses. This seems logical at some initial level, but constructing such a prior for convoluted hypotheses may simply be impossible… Because the null hypothesis has a positive mass (maybe .5) under the “unconstrained prior” (p.48), the author can also get away with projecting this prior onto the constrained space of the null hypothesis. Even when setting the prior variance to oo (p.50). The Bayes factor is then the ratio of the (posterior and prior) normalising constants over the constrained parameter space. The book still mentions the Lindley-Bartlett paradox (p.60) in the case of the about equality hypotheses. The appendix to this chapter mentions the issue of improper priors and the need for accommodating infinite mass with training samples, providing a minimum training sample solution using mixtures that sound fairly ad hoc to me.

“Bayes factors for the evaluation of informative hypotheses have a simple form.” (p. 193)

Chapter 10 is the final chapter of Informative Hypotheses, on “Foundations of Bayesian evaluation of informative hypotheses”, and I was expecting a more in-depth analysis of those special hypotheses, but it is mostly a repetition of what is found in Chapter 3, the wider generality being never exploited to a useful depth. There is also this gem quoted above  that, because Bayes factors are the ratio of two (normalising) constants, f_m/c_m, they have a “simple form”. The reference to Carlin and Chib (1995) for computing other cases then sounds pretty obscure. (Another tiny gem is that I spotted the R software contingency spelled with three different spellings.)  The book mentions the Savage-Dickey representation of the Bayes factor, but I could not spot the connection from the few lines (p.193) dedicated to this ratio. More generally, I do not find the generality of this chapter particularly convincing, most of it replicating the notions found in Chapter 3., like the use of posterior priors. The numerical approximation of Bayes factors is proposed via simulation from the unconstrained prior and posterior (p.207) then via a stepwise decomposition of the Bayes factor (p.208) and a Gibbs sampler that relies on inverse cdf sampling.

Overall, I feel that this book came out too early, without a proper basis and dissemination of the ideas of the author: to wit, a large number of references are connected to the author, some In Press, other Unpublished (which leads to a rather abstract “see Hoijtink (Unpublished) for a related theorem” (p.195)). From my incomplete reading, I did not gather a sense of novel perspective but rather of a topic that seemed too narrow for a whole book.

Statistics, with interactions

Due to a tight June schedule (3rd conference in a week!), I only stayed one day at the SIOD 2013 conference in Saigon. (SIOD means Statistics and interaction with other disciplines.) The conference was housed by Ton Duc Thang University, on a very modern campus, and it sounded like the university had drafted a lot of his undergrads to catter to the SIOD participants: similar to the Bayesian conference in India a few months ago, those students would stand at the ready to guide us around the campus and to relay any problem to the organisers. This was very helpful and enjoyable, a plus being that most female students wore the traditional pink costume adopted by the university, but it also made me a wee bit uncomfortable as I do not know how much say those students had in this draft… In particular, most of the students I talked with were from other fields than Statistics. (And definitely not complaining, but being on the opposite very friendly the whole time!) A funny side story is that I got a wake-up call from the conference organisers in the morning as I had missed a welcome ceremony with the president due to oversleeping (itself due to an excess of iced coffee rather than minimal jetlag!). Among the few talks I attended, some French school statistics due to the presence of a large contingent from Toulouse, a talk about zero inflated normal distributions which sounded like missing-at-random normal observations (hence easy to process), and a talk about the point of using Bayes factors in hypothesis testing which essentially if independently provided a second version of my course from the previous day.

Yesterday, I also had a short discussion with Paul Minh who presented a talk on a general regenerative device for MCMC algorithms, using a bound on the target density rather than on the Markov transition in order to achieve easier regeneration. While a neat idea, this method requires the construction of a lower bound that can easily simulated. Furthermore, if the regeneration probability is low, the mixing speed may remain similar to the original MCMC sampler, as the method ressorts to a standard MCMC step on the remaining part of the target density.