This paper by Andrew Gelman and Christian Hennig calls for the abandonment of the terms objective and subjective in (not solely Bayesian) statistics. And argue that there is more than mere prior information and data to the construction of a statistical analysis. The paper is articulated as the authors’ proposal, followed by four application examples, then a survey of the philosophy of science perspectives on objectivity and subjectivity in statistics and other sciences, next to a study of the subjective and objective aspects of the mainstream statistical streams, concluding with a discussion on the implementation of the proposed move. Continue reading
Archive for frequentist inference
The workshop at the BIPM on measurement uncertainty was certainly most exciting, first by its location in the Parc de Saint Cloud in classical buildings overlooking the Seine river in a most bucolic manner…and second by its mostly Bayesian flavour. The recommendations that the workshop addressed are about revisions in the current GUM, which stands for the Guide to the Expression of Uncertainty in Measurement. The discussion centred on using a more Bayesian approach than in the earlier version, with the organisers of the workshop and leaders of the revision apparently most in favour of that move. “Knowledge-based pdfs” came into the discussion as an attractive notion since it rings a Bayesian bell, especially when associated with probability as a degree of belief and incorporating the notion of an a priori probability distribution. And propagation of errors. Or even more when mentioning the removal of frequentist validations. What I gathered from the talks is the perspective drifting away from central limit approximations to more realistic representations, calling for Monte Carlo computations. There is also a lot I did not get about conventions, codes and standards. Including a short debate about the different meanings on Monte Carlo, from simulation technique to calculation method (as for confidence intervals). And another discussion about replacing the old formula for estimating sd from the Normal to the Student’s t case. A change that remains highly debatable since the Student’s t assumption is as shaky as the Normal one. What became clear [to me] during the meeting is that a rather heated debate is currently taking place about the need for a revision, with some members of the six (?) organisations involved arguing against Bayesian or linearisation tools.
This became even clearer during our frequentist versus Bayesian session with a first talk so outrageously anti-Bayesian it was hilarious! Among other things, the notion that “fixing” the data was against the principles of physics (the speaker was a physicist), that the only randomness in a Bayesian coin tossing was coming from the prior, that the likelihood function was a subjective construct, that the definition of the posterior density was a generalisation of Bayes’ theorem [generalisation found in… Bayes’ 1763 paper then!], that objective Bayes methods were inconsistent [because Jeffreys’ prior produces an inadmissible estimator of μ²!], that the move to Bayesian principles in GUM would cost the New Zealand economy 5 billion dollars [hopefully a frequentist estimate!], &tc., &tc. The second pro-frequentist speaker was by comparison much much more reasonable, although he insisted on showing Bayesian credible intervals do not achieve a nominal frequentist coverage, using a sort of fiducial argument distinguishing x=X+ε from X=x+ε that I missed… A lack of achievement that is fine by my standards. Indeed, a frequentist confidence interval provides a coverage guarantee either for a fixed parameter (in which case the Bayesian approach achieves better coverage by constant updating) or a varying parameter (in which case the frequency of proper inclusion is of no real interest!). The first Bayesian speaker was Tony O’Hagan, who summarily shred the first talk to shreds. And also criticised GUM2 for using reference priors and maxent priors. I am afraid my talk was a bit too exploratory for the audience (since I got absolutely no question!) In retrospect, I should have given an into to reference priors.
An interesting specificity of a workshop on metrology and measurement is that they are hard stickers to schedule, starting and finishing right on time. When a talk finished early, we waited until the intended time to the next talk. Not even allowing for extra discussion. When the only overtime and Belgian speaker ran close to 10 minutes late, I was afraid he would (deservedly) get lynched! He escaped unscathed, but may (and should) not get invited again..!
I found another paper on the Jeffreys-Lindley paradox. Entitled “A Misleading Intuition and the Bayesian Blind Spot: Revisiting the Jeffreys-Lindley’s Paradox”. Written by Guillaume Rochefort-Maranda, from Université Laval, Québec.
This paper starts by assuming an unbiased estimator of the parameter of interest θ and under test for the null θ=θ0. (Which makes we wonder at the reason for imposing unbiasedness.) Another highly innovative (or puzzling) aspect is that the Lindley-Jeffreys paradox presented therein is described without any Bayesian input. The paper stands “within a frequentist (classical) framework”: it actually starts with a confidence-interval-on-θ-vs.-test argument to argue that, with a fixed coverage interval that excludes the null value θ0, the estimate of θ may converge to θ0 without ever accepting the null θ=θ0. That is, without the confidence interval ever containing θ0. (Although this is an event whose probability converges to zero.) Bayesian aspects come later in the paper, even though the application to a point null versus a point null test is of little interest since a Bayes factor is then a likelihood ratio.
As I explained several times, including in my Philosophy of Science paper, I see the Lindley-Jeffreys paradox as being primarily a Bayesiano-Bayesian issue. So just the opposite of the perspective taken by the paper. That frequentist solutions differ does not strike me as paradoxical. Now, the construction of a sequence of samples such that all partial samples in the sequence exclude the null θ=θ0 is not a likely event, so I do not see this as a paradox even or especially when putting on my frequentist glasses: if the null θ=θ0 is true, this cannot happen in a consistent manner, even though a single occurrence of a p-value less than .05 is highly likely within such a sequence.
Unsurprisingly, the paper relates to the three most recent papers published by Philosophy of Science, discussing first and foremost Spanos‘ view. When the current author introduces Mayo and Spanos’ severity, i.e. the probability to exceed the observed test statistic under the alternative, he does not define this test statistic d(X), which makes the whole notion incomprehensible to a reader not already familiar with it. (And even for one familiar with it…)
“Hence, the solution I propose (…) avoids one of [Freeman’s] major disadvantages. I suggest that we should decrease the size of tests to the extent where it makes practically no difference to the power of the test in order to improve the likelihood ratio of a significant result.” (p.11)
One interesting if again unsurprising point in the paper is that one reason for the paradox stands in keeping the significance level constant as the sample size increases. While it is possible to decrease the significance level and to increase the power simultaneously. However, the solution proposed above does not sound rigorous hence I fail to understand how low the significance has to be for the method to stop/work. I cannot fathom a corresponding algorithmic derivation of the author’s proposal.
“I argue against the intuitive idea that a significant result given by a very powerful test is less convincing than a significant result given by a less powerful test.”
The criticism on the “blind spot” of the Bayesian approach is supported by an example where the data is issued from a distribution other than either of the two tested distributions. It seems reasonable that the Bayesian answer fails to provide a proper answer in this case. Even though it illustrates the difficulty with the long-term impact of the prior(s) in the Bayes factor and (in my opinion) the need to move away from this solution within the Bayesian paradigm.
“In place of past experience, frequentism considers future behavior: an optimal estimator is one that performs best in hypothetical repetitions of the current experiment. The resulting gain in scientific objectivity has carried the day…”
Julien Cornebise sent me this Science column by Brad Efron about Bayes’ theorem. I am a tad surprised that it got published in the journal, given that it does not really contain any new item of information. However, being unfamiliar with Science, it may also be that it also publishes major scientists’ opinions or warnings, a label that can fit this column in Science. (It is quite a proper coincidence that the post appears during Bayes 250.)
Efron’s piece centres upon the use of objective Bayes approaches in Bayesian statistics, for which Laplace was “the prime violator”. He argues through examples that noninformative “Bayesian calculations cannot be uncritically accepted, and should be checked by other methods, which usually means “frequentistically”. First, having to write “frequentistically” once is already more than I can stand! Second, using the Bayesian framework to build frequentist procedures is like buying top technical outdoor gear to climb the stairs at the Sacré-Coeur on Butte Montmartre! The naïve reader is then left clueless as to why one should use a Bayesian approach in the first place. And perfectly confused about the meaning of objectivity. Esp. given the above quote! I find it rather surprising that this old saw of a claim of frequentism to objectivity resurfaces there. There is an infinite range of frequentist procedures and, while some are more optimal than others, none is “the” optimal one (except for the most baked-out examples like say the estimation of the mean of a normal observation).
“A Bayesian FDA (there isn’t one) would be more forgiving. The Bayesian posterior probability of drug A’s superiority depends only on its final evaluation, not whether there might have been earlier decisions.”
The second criticism of Bayesianism therein is the counter-intuitive irrelevance of stopping rules. Once again, the presentation is fairly biased, because a Bayesian approach opposes scenarii rather than evaluates the likelihood of a tail event under the null and only the null. And also because, as shown by Jim Berger and co-authors, the Bayesian approach is generally much more favorable to the null than the p-value.
“Bayes’ Theorem is an algorithm for combining prior experience with current evidence. Followers of Nate Silver’s FiveThirtyEight column got to see it in spectacular form during the presidential campaign: the algorithm updated prior poll results with new data on a daily basis, nailing the actual vote in all 50 states.”
It is only fair that Nate Silver’s book and column are mentioned in Efron’s column. Because it is a highly valuable and definitely convincing illustration of Bayesian principles. What I object to is the criticism “that most cutting-edge science doesn’t enjoy FiveThirtyEight-level background information”. In my understanding, the poll model of FiveThirtyEight built up in a sequential manner a weight system over the different polling companies, hence learning from the data if in a Bayesian manner about their reliability (rather than forgetting the past). This is actually what caused Larry Wasserman to consider that Silver’s approach was actually more frequentist than Bayesian…
“Empirical Bayes is an exciting new statistical idea, well-suited to modern scientific technology, saying that experiments involving large numbers of parallel situations carry within them their own prior distribution.”
My last point of contention is about the (unsurprising) defence of the empirical Bayes approach in the Science column. Once again, the presentation is biased towards frequentism: in the FDR gene example, the empirical Bayes procedure is motivated by being the frequentist solution. The logical contradiction in “estimat[ing] the relevant prior from the data itself” is not discussed and the conclusion that Brad Efron uses “empirical Bayes methods in the parallel case [in the absence of prior information”, seemingly without being cautious and “uncritically”, does not strike me as the proper last argument in the matter! Nor does it give a 21st Century vision of what nouveau Bayesianism should be, faced with the challenges of Big Data and the like…
You assume that I am interested in long-term average properties of procedures, even though I have so often argued that they are at most necessary (as consequences of good procedures), but scarcely sufficient for a severity assessment. The error statistical account I have developed is a statistical philosophy. It is not one to be found in Neyman and Pearson, jointly or separately, except in occasional glimpses here and there (unfortunately). It is certainly not about well-defined accept-reject rules. If N-P had only been clearer, and Fisher better behaved, we would not have had decades of wrangling. However, I have argued, the error statistical philosophy explicates, and directs the interpretation of, frequentist sampling theory methods in scientific, as opposed to behavioural, contexts. It is not a complete philosophy…but I think Gelmanian Bayesians could find in it a source of “standard setting”.
You say “the prior is both a probabilistic object, standard from this perspective, and a subjective construct, translating qualitative personal assessments into a probability distribution. The extension of this dual nature to the so-called “conventional” priors (a very good semantic finding!) is to set a reference … against which to test the impact of one’s prior choices and the variability of the resulting inference. …they simply set a standard against which to gauge our answers.”
I think there are standards for even an approximate meaning of “standard-setting” in science, and I still do not see how an object whose meaning and rationale may fluctuate wildly, even in a given example, can serve as a standard or reference. For what?
Perhaps the idea is that one can gauge how different priors change the posteriors, because, after all, the likelihood is well-defined. That is why the prior and not the likelihood is the camel. But it isn’t obvious why I should want the camel. (camel/gnat references in the paper and response).
While preparing a book chapter, I checked on Google Ngram viewer the comparative uses of the words Bayesian (blue), maximum likelihood (red) and frequentist (yellow), producing the above (screen-copy quality, I am afraid!). It shows an increase of the use of the B word from the early 80’s and not the sudden rise in the 90’s I was expecting. The inclusion of “frequentist” is definitely in the joking mode, as this is not a qualification used by frequentists to describe their methods. In other words (!), “frequentist” does not occur very often in frequentist papers (and not as often as in Bayesian papers!)…
As I attended Jamie Robins’ session in Varanasi and did not have a clear enough idea of the Robbins and Wasserman paradox to discuss it viva vocce, here are my thoughts after reading Larry’s summary. My first reaction was to question whether or not this was a Bayesian statistical problem (meaning why should I be concered with the problem). Just as the normalising constant problem was not a statistical problem. We are estimating an integral given some censored realisations of a binomial depending on a covariate through an unknown function θ(x). There is not much of a parameter. However, the way Jamie presented it thru clinical trials made the problem sound definitely statistical. So end of the silly objection. My second step is to consider the very point of estimating the entire function (or infinite dimensional parameter) θ(x) when only the integral ψ is of interest. This is presumably the reason why the Bayesian approach fails as it sounds difficult to consistently estimate θ(x) under censored binomial observations, while ψ can be. Of course, if we want to estimate the probability of a success like ψ going through functional estimation this sounds like overshooting. But the Bayesian modelling of the problem appears to require considering all unknowns at once, including the function θ(x) and cannot forget about it. We encountered a somewhat similar problem with Jean-Michel Marin when working on the k-nearest neighbour classification problem. Considering all the points in the testing sample altogether as unknowns would dwarf the training sample and its information content to produce very poor inference. And so we ended up dealing with one point at a time after harsh and intense discussions! Now, back to the Robins and Wasserman paradox, I see no problem in acknowledging a classical Bayesian approach cannot produce a convergent estimate of the integral ψ. Simply because the classical Bayesian approach is an holistic system that cannot remove information to process a subset of the original problem. Call it the curse of marginalisation. Now, on a practical basis, would there be ways of running simulations of the missing Y’s when π(x) is known in order to achieve estimates of ψ? Presumably, but they would end up with a frequentist validation…