My Journey From Frequentist to Bayesian Statistics

Type I error for smoke detector: probability of alarm given no fire=0.05
Bayesian: probability of fire given current air data

Frequentist smoke alarm designed as most research is done:
Set the alarm trigger so as to have a 0.8 chance of detecting an inferno

Advantage of actionable evidence quantification:
Set the alarm to trigger when the posterior probability of a fire exceeds 0.02 while at home and at 0.01 while away

If I had been taught Bayesian modeling before being taught the frequentist paradigm, I'm sure I would have always been a Bayesian.  I started becoming a Bayesian about 1994 because of an influential paper by David Spiegelhalter and because I worked in the same building at Duke University as Don Berry.  Two other things strongly contributed to my thinking: difficulties explaining p-values and confidence intervals (especially the latter) to clinical researchers, and difficulty of learning group sequential methods in clinical trials.  When I talked with Don and learned about the flexibility of the Bayesian approach to clinical trials, and saw Spiegelhalter's embrace of Bayesian methods because of its problem-solving abilities, I was hooked.  [Note: I've heard Don say that he became Bayesian after multiple attempts to teach statistics students the exact definition of a confidence interval.  He decided the concept was defective.]

At the time I was working on clinical trials at Duke and started to see that multiplicity adjustments were arbitrary.  This started with a clinical trial coordinated by Duke in which low dose and high dose of a new drug were to be compared to placebo, using an alpha cutoff of 0.03 for each comparison to adjust for multiplicity.  The comparison of high dose with placebo resulted in a p-value of 0.04 and the trial was labeled completely "negative" which seemed problematic to me. [Note: the p-value was two-sided and thus didn't give any special "credit" for the treatment effect coming out in the right direction.]

I began to see that the hypothesis testing framework wasn't always the best approach to science, and that in biomedical research the typical hypothesis was an artificial construct designed to placate a reviewer who believed that an NIH grant's specific aims must include null hypotheses.  I saw the contortions that investigators went through to achieve this, came to see that questions are more relevant than hypotheses, and estimation was even more important than questions.   With Bayes, estimation is emphasized.  I very much like Bayesian modeling instead of hypothesis testing.  I saw that a large number of clinical trials were incorrectly interpreted when p>0.05 because the investigators involved failed to realize that a p-value can only provide evidence against a hypothesis. Investigators are motivated by "we spent a lot of time and money and must have gained something from this experiment." The classic "absence of evidence is not evidence of absence" error results, whereas with Bayes it is easy to estimate the probability of similarity of two treatments.  Investigators will be surprised to know how little we have learned from clinical trials that are not huge when p>0.05.

I listened to many discussions of famous clinical trialists debating what should be the primary endpoint in a trial, the co-primary endpoint, the secondary endpoints, co-secondary endpoints, etc.  This was all because of their paying attention to alpha-spending.  I realized this was all a game.

I came to not believe in the possibility of infinitely many repetitions of identical experiments, as required to be envisioned in the frequentist paradigm.  When I looked more thoroughly into the multiplicity problem, and sequential testing, and I looked at Bayesian solutions, I became more of a believer in the approach.  I learned that posterior probabilities have a simple interpretation independent of the stopping rule and frequency of data looks.  I got involved in working with the FDA and then consulting with pharmaceutical companies, and started observing how multiple clinical endpoints were handled.  I saw a closed testing procedures where a company was seeking a superiority claim for a new drug, and if there was insufficient evidence for such a claim, they wanted to seek a non-inferiority claim on another endpoint.  They developed a closed testing procedure that when diagrammed truly looked like a train wreck.  I felt there had to be a better approach, so I sought to see how far posterior probabilities could be pushed.  I found that with MCMC simulation of Bayesian posterior draws I could quite simply compute probabilities such as P(any efficacy), P(efficacy more than trivial), P(non-inferiority), P(efficacy on endpoint A and on either endpoint B or endpoint C), and P(benefit on more than 2 of 5 endpoints).  I realized that frequentist multiplicity problems came from the chances you give data to be more extreme, not from the chances you give assertions to be true.

I enjoy the fact that posterior probabilities define their own error probabilities, and that they count not only inefficacy but also harm.  If P(efficacy)=0.97, P(no effect or harm)=0.03.  This is the "regulator's regret", and type I error is not the error of major interest (is it really even an 'error'?).  One minus a p-value is P(data in general are less extreme than that observed if H0 is true) which is the probability of an event I'm not that interested in.

The extreme amount of time I spent analyzing data led me to understand other problems with the frequentist approach.  Parameters are either in a model or not in a model.  We test for interactions with treatment and hope that the p-value is not between 0.02 and 0.2.  We either include the interactions or exclude them, and the power for the interaction test is modest.  Bayesians have a prior for the differential treatment effect and can easily have interactions "half in" the model.  Dichotomous irrevocable decisions are at the heart of many of the statistical modeling problems we have today.  I really like penalized maximum likelihood estimation (which is really empirical Bayes) but once we have a penalized model all of our frequentist inferential framework fails us.  No one can interpret a confidence interval for a biased (shrunken; penalized) estimate.  On the other hand, the Bayesian posterior probability density function, after shrinkage is accomplished using skeptical priors, is just as easy to interpret as had the prior been flat.  For another example, consider a categorical predictor variable that we hope is predicting in an ordinal (monotonic) fashion.  We tend to either model it as ordinal or as completely unordered (using k-1 indicator variables for k categories).  A Bayesian would say "let's use a prior that favors monotonicity but allows larger sample sizes to override this belief."

Now that adaptive and sequential experiments are becoming more popular, and a formal mechanism is needed to use data from one experiment to inform a later experiment (a good example being the use of adult clinical trial data to inform clinical trials on children when it is difficult to enroll a sufficient number of children for the child data to stand on their own), Bayes is needed more than ever.  It took me a while to realize something that is quite profound: A Bayesian solution to a simple problem (e.g., 2-group comparison of means) can be embedded into a complex design (e.g., adaptive clinical trial) without modification.  Frequentist solutions require highly complex modifications to work in the adaptive trial setting.

I met likelihoodist Jeffrey Blume in 2008 and started to like the likelihood approach.  It is more Bayesian than frequentist.  I plan to learn more about this paradigm. 

Several readers have asked me how I could believe all this and publish a frequentist-based book such as Regression Modeling Strategies.  There are two primary reasons.  First, I started writing the book before I knew much about Bayes.  Second, I performed a lot of simulation studies that showed that purely empirical model-building had a low chance of capturing clinical phenomena correctly and of validating on new datasets.  I worked extensively with cardiologists such as Rob Califf, Dan Mark, Mark Hlatky, David Prior, and Phil Harris who give me the ideas for injecting clinical knowledge into model specification.  From that experience I wrote Regression Modeling Strategies in the most Bayesian way I could without actually using specific  Bayesian methods.  I did this by emphasizing subject-matter-guided model specification.  The section in the book about specification of interaction terms is perhaps the best example.  When I teach the full-semester version of my course I interject Bayesian counterparts to many of the techniques covered.

There are challenges in moving more to a Bayesian approach.  The ones I encounter most frequently are:

1. Teaching clinical trialists to embrace Bayes when they already do in spirit but not operationally.  Unlearning things is much more difficult than learning things.
2. How to work with sponsors, regulators, and NIH principal investigators to specify the (usually skeptical) prior up front, and to specify the amount of applicability assumed for previous data.
3. What is a Bayesian version of the multiple degree of freedom "chunk test"?  Partitioning sums of squares or the log likelihood into components, e.g., combined test of interaction and combined test of nonlinearities, is very easy and natural in the frequentist setting.
4. How do we specify priors for complex entities such as the degree of monotonicity of the effect of a continuous predictor in a regression model?  The Bayesian approach to this will ultimately be more satisfying, but operationalizing this is not easy.

With new tools such as Stan and well written accessible books such as Kruschke's it's getting to be easier to be Bayesian each day.  The R brms package, which uses Stan, makes a large class of regression models even more accessible.

Update 2017-12-29

Another reason for moving from frequentism to Bayes is that frequentist ideas are so confusing that even expert statisticians frequently misunderstand them, and are tricked into dichotomous thinking because of the adoption of null hypothesis significance testing (NHST).   The paper by BB McShane and D Gal in JASA demonstrates alarming errors in interpretation by many authors of JASA papers.  If those with a high level of statistical training make frequent interpretation errors could frequentist statistics be fundamentally flawed?  Yes!  In McShane and Gal's paper they described two surveys sent to authors of JASA, as well as to authors of articles not appearing in the statistical literature (luckily for statisticians the non-statisticians fared a bit worse).   Some of their key findings are as follows.

1. When a p-value is present, (primarily frequentist) statisticians confuse population vs. sample, especially if the p-value is large.  Even when directly asked whether patients in this sample fared batter on one treatment than the other, the respondents often answered according to whether or not p < 0.05.  Dichotomous thinking crept in.
2. When asked whether evidence from the data made it more or less likely that a drug is beneficial in the population, many statisticians again were swayed by the p-value and not tendencies indicated by the raw data.  The failed to understand that your chances are improved by "playing the odds", and gave different answers whether one was playing the odds for an unknown person vs. selecting treatment for themselves.
3. In previous studies by the authors, they found that "applied researchers presented with not only a p-value but also with a posterior probability based on a noninformative prior were less likely to make dichotomization errors."

The authors also echoed Wasserstein, Lazar, and Cobb's concern that we are setting researchers up for failure: "we teach NHST because that's what the scientific community and journal editors use but they use NHST because that's what we teach them.  Indeed, statistics at the undergraduate level as well as at the graduate level in applied fields is often taught in a rote and recipe-like manner that typically focuses exclusively on the NHST paradigm."

Some of the problems with frequentist statistics are the way in which its methods are misused, especially with regard to dichotomization.  But an approach that is so easy to misuse and which sacrifices direct inference in a futile attempt at objectivity still has fundamental problems.

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Clinicians' Misunderstanding of Probabilities Makes Them Like Backwards Probabilities Such As Sensitivity, Specificity, and Type I Error

Imaging watching a baseball game, seeing the batter get a hit, and hearing the announcer say "The chance that the batter is left handed is now 0.2!"   No one would care.  Baseball fans are interested in the chance that a batter will get a hit conditional on his being right handed (handedness being already known to the fan), the handedness of the pitcher, etc.  Unless one is an archaeologist or medical examiner, the interest is in forward probabilities conditional on current and past states.  We are interested in the probability of the unknown given the known and the probability of a future event given past and present conditions and events.

Clinicians are people trained in the science and practice of medicine, and most of them are very good at it.  They are also very good at many aspects of research.  But they are generally not taught probability, and this can limit their research skills.  Many excellent clinicians even let their limitations in understanding probability make them believe that their clinical decision making is worse than it actually is.  I have taught many clinicians who say "I need a hard and fast rule so I know how to diagnosis or treat patients.  I need a hard cutoff on blood pressure, HbA1c, etc. so that I know what to do, and the fact that I either treat or not treat the patient means that I don't want to consider a probability of disease but desire a simple classification rule."  This makes the clinician try to influence the statistician to use inefficient, arbitrary methods such as categorization, stratification, and matching.

In reality, clinicians do not act that way when treating patients.  They are smart enough to know that if a patient has cholesterol just over someone's arbitrary threshold they may not start statin therapy right away if the patient has no other risk factors (e.g., smoking) going against him.  They know that sometimes you start a patient on a lower dose and see how she responds, or start one drug and try it for a while and then switch drugs if the efficacy is unacceptable or there is a significant side effect.

So I emphasize the need to understand probabilities when I'm teaching clinicians.  A probability is a self-contained summary of the current information, except for the patient's risk aversion and other utilities.  Clinicians need to be comfortable with a probability of 0.5 meaning "we don't know much" and not requesting a classification of disease/normal that does nothing but cover up the problem.  A classification does not account for gray zones or patient and physician utility functions.

Even physicians who understand the meaning of a probability are often not understanding conditioning.  Conditioning is all important, and conditioning on different things massively changes the meaning of the probabilities being computed.  Every physician I've known has been taught probabilistic medical diagnosis by first learning about sensitivity (sens) and specificity (spec).  These are probabilities that are in backwards time- and information flow order.  How did this happen? Sensitivity, specificity, and receiver operating characteristic curves were developed for radar and radio research in the military.  It was a important to receive radio signals from distant aircraft, and to detect an incoming aircraft on radar.  The ability to detect something that is really there is definitely important.  In the 1950s, virologists appropriated these concepts to measure the performance of viral cultures.  Virus needs to be detected when it's present, and not detected when it's not.  Sensitivity is the probability of detecting a condition when it is truly present, and specificity is the probability of not detecting it when it is truly absent.  One can see how these probabilities would be useful outside of virology and bacteriology when the samples are retrospective, as in a case-control studies.  But I believe that clinicians and researchers would be better off if backward probabilities were not taught or were mentioned only to illustrate how not to think about a problem.

But the way medical students are educated, they assume that sens and spec are what you first consider in a prospective cohort of patients!  This gives the professor the opportunity of teaching  Bayes' rule and requires the use of a supposedly unconditional probability known as prevalence which is actually not very well defined.  The students plugs everything into Bayes' rule and fails to notice that several quantities cancel out.  The result is the following: the proportion of patients with a positive test who have disease, and the proportion with a negative test who have disease.  These are trivially calculated from the cohort data without knowing anything about sens, spec, and Bayes.  This way of thinking harms the student's understanding for years to come and influences those who later engage in clinical and pharmaceutical research to believe that type I error and p-values are directly useful.

The situation in medical diagnosis gets worse when referral bias (also called workup bias) is present.  When certain types of patients do not get a final diagnosis, sens and spec are biased.  For example, younger women with a negative test may not get the painful procedure that yields the final diagnosis.  There are formulas that must be used to correct sens and spec.  But wait!  When Bayes' rule is used to obtain the probability of disease we needed in the first place, these corrections completely cancel out when the usual correction methods are used!  Using forward probabilities in the first place means that one just conditions on age, sex, and result of the initial diagnostic test and no special methods other than (sometimes) logistic regression are required.

There is an analogy to statistical testing.  p-values and type I error are affected by sequential testing and a host of other factors, but forward-time probabilities (Bayesian posterior probabilities) are not.  Posterior probabilities condition on what is known and does not have to imagine alternate paths to getting to what is known (as do sens and spec when workup bias exists).  p-values and type I errors are backwards-information-flow measures, and clinical researchers and regulators come to believe that type I error is the error of interest.  They also very frequently misinterpret p-values.  The p-value is one minus spec, and power is sens.  The posterior probability is exactly analogous to the probability of disease.

Sens and spec are so pervasive in medicine, bioinformatics, and biomarker research that we don't question how silly they would be in other contexts.  Do we dichotomize a response variable so that we can compute the probability that a patient is on treatment B given a "positive" response?  On the contrary we want to know the full continuous distribution of the response given the assigned treatment.  Again this represents forward probabilities.