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.

---

Interactive Statistical Graphics: Showing More By Showing Less

Version 4 of the R Hmisc packge and version 5 of the R rms package interfaces with interactive plotly graphics, which is an interface to the D3 javascript graphics library.  This allows various results of statistical analyses to be viewed interactively, with pre-programmed drill-down information.  More examples will be added here.  We start with a video showing a new way to display survival curves.

Note that plotly graphics are best used with RStudio Rmarkdown html notebooks, and are distributed to reviewers as self-contained (but somewhat large) html files. Printing is discouraged, but possible, using snapshots of the interactive graphics.

Concerning the second bullet point below, boxplots have a high ink:information ratio and hide bimodality and other data features.  Many statisticians prefer to use dot plots and violin plots.  I liked those methods for a while, then started to have trouble with the choice of a smoothing bandwidth in violin plots, and found that dot plots do not scale well to very large datasets, whereas spike histograms are useful for all sample sizes.  Users of dot charts have to have a dot stand for more than one observation if N is large, and I found the process too arbitrary.  For spike histograms I typically use 100 or 200 bins.  When the number of distinct data values is below the specified number of bins, I just do a frequency tabulation for all distinct data values, rounding only when two of the values are very close to each other.  A spike histogram approximately reduces to a rug plot when there are no ties in the data, and I very much like rug plots.

• rms survplotp video: plotting survival curves
• Hmisc histboxp interactive html example: spike histograms plus selected quantiles, mean, and Gini's mean difference - replacement for boxplots - show all the data!  Note bimodal distributions and zero blood pressure values for patients having a cardiac arrest.

A Litany of Problems With p-values

In my opinion, null hypothesis testing and p-values have done significant harm to science.  The purpose of this note is to catalog the many problems caused by p-values.  As readers post new problems in their comments, more will be incorporated into the list, so this is a work in progress.

The American Statistical Association has done a great service by issuing its Statement on Statistical Significance and P-values.  Now it's time to act.  To create the needed motivation to change, we need to fully describe the depth of the problem.

It is important to note that no statistical paradigm is perfect.  Statisticians should choose paradigms that solve the greatest number of real problems and have the fewest number of faults.  This is why I believe that the Bayesian and likelihood paradigms should replace frequentist inference.

Consider an assertion such as "the coin is fair", "treatment A yields the same blood pressure as treatment B", "B yields lower blood pressure than A", or "B lowers blood pressure at least 5mmHg before A."  Consider also a compound assertion such as "A lowers blood pressure by at least 3mmHg and does not raise the risk of stroke."

A. Problems With Conditioning

1. p-values condition on what is unknown (the assertion of interest; H₀) and do not condition on what is known (the data).
2. This conditioning does not respect the flow of time and information; p-values are backward probabilities.

B. Indirectness

1. Because of A above, p-values provide only indirect evidence and are problematic as evidence metrics.  They are sometimes monotonically related to the evidence (e.g., when the prior distribution is flat) we need but are not properly calibrated for decision making.
2. p-values are used to bring indirect evidence against an assertion but cannot bring evidence in favor of the assertion.  
3. As detailed here, the idea of proof by contradiction is a stretch when working with probabilities, so trying to quantify evidence for an assertion by bringing evidence against its complement is on shaky ground.
4. Because of A, p-values are difficult to interpret and very few non-statisticians get it right.  The best article on misinterpretations I've found is here.

C. Problem Defining the Event Whose Probability is Computed

1. In the continuous data case, the probability of getting a result as extreme as that observed with our sample is zero, so the p-value is the probability of getting a result more extreme than that observed.  Is this the correct point of reference?
2. How does more extreme get defined if there are sequential analyses and multiple endpoints or subgroups?  For sequential analyses do we consider planned analyses are analyses intended to be run even if they were not?

D. Problems Actually Computing p-values

1. In some discrete data cases, e.g., comparing two proportions, there is tremendous disagreement among statisticians about how p-values should be calculated.  In a famous 2x2 table from an ECMO adaptive clinical trial, 13 p-values have been computed from the same data, ranging from 0.001 to 1.0.  And many statisticians do not realize that Fisher's so-called "exact" test is not very accurate in many cases.
2. Outside of binomial, exponential, and normal (with equal variance) and a few other cases, p-values are actually very difficult to compute exactly, and many p-values computed by statisticians are of unknown accuracy (e.g., in logistic regression and mixed effects models). The more non-quadratic the log likelihood function the more problematic this becomes in many cases. 
3. One can compute (sometimes requiring simulation) the type-I error of many multi-stage procedures, but actually computing a p-value that can be taken out of context can be quite difficult and sometimes impossible.  One example: one can control the false discovery probability (incorrectly usually referred to as a rate), and ad hoc modifications of nominal p-values have been proposed, but these are not necessarily in line with the real definition of a p-value.

E. The Multiplicity Mess

1. Frequentist statistics does not have a recipe or blueprint leading to a unique solution for multiplicity problems, so when many p-values are computed, the way they are penalized for multiple comparisons results in endless arguments.  A Bonferroni multiplicity adjustment is consistent with a Bayesian prior distribution specifying that the probability that all null hypotheses are true is a constant no matter how many hypotheses are tested.  By contrast, Bayesian inference reflects the facts that P(A ∪ B) ≥ max(P(A), P(B)) and P(A ∩ B) ≤ min(P(A), P(B)) when A and B are assertions about a true effect.
2. There remains controversy over the choice of 1-tailed vs. 2-tailed tests.  The 2-tailed test can be thought of as a multiplicity penalty for being potentially excited about either a positive effect or a negative effect of a treatment.  But few researchers want to bring evidence that a treatment harms patients; a pharmaceutical company would not seek a licensing claim of harm.  So when one computes the probability of obtaining an effect larger than that observed if there is no true effect, why do we too often ignore the sign of the effect and compute the (2-tailed) p-value?
3. Because it is a very difficult problem to compute p-values when the assertion is compound, researchers using frequentist methods do not attempt to provide simultaneous evidence regarding such assertions and instead rely on ad hoc multiplicity adjustments.
4. Because of A1, statistical testing with multiple looks at the data, e.g., in sequential data monitoring, is ad hoc and complex.  Scientific flexibility is discouraged.  The p-value for an early data look must be adjusted for future looks.  The p-value at the final data look must be adjusted for the earlier inconsequential looks.  Unblinded sample size re-estimation is another case in point.  If the sample size is expanded to gain more information, there is a multiplicity problem and some of the methods commonly used to analyze the final data effectively discount the first wave of subjects.  How can that make any scientific sense?
5. Most practitioners of frequentist inference do not understand that multiplicity comes from chances you give data to be extreme, not from chances you give true effects to be present.

F. Problems With Non-Trivial Hypotheses

1. It is difficult to test non-point hypotheses such as "drug A is similar to drug B".
2. There is no straightforward way to test compound hypotheses coming from logical unions and intersections. 

G. Inability to Incorporate Context and Other Information

1. Because extraordinary claims require extraordinary evidence, there is a serious problem with the p-value's inability to incorporate context or prior evidence.  A Bayesian analysis of the existence of ESP would no doubt start with a very skeptical prior that would require extraordinary data to overcome, but the bar for getting a "significant" p-value is fairly low. Frequentist inference has a greater risk for getting the direction of an effect wrong (see here for more).
2. p-values are unable to incorporate outside evidence.  As a converse to 1, strong prior beliefs are unable to be handled by p-values, and in some cases the results in a lack of progress.  Nate Silver in The Signal and the Noise beautifully details how the conclusion that cigarette smoking causes lung cancer was greatly delayed (with a large negative effect on public health) because scientists (especially Fisher) were caught up in the frequentist way of thinking, dictating that only randomized trial data would yield a valid p-value for testing cause and effect.  A Bayesian prior that was very strongly against the belief that smoking was causal is obliterated by the incredibly strong observational data.  Only by incorporating prior skepticism could one make a strong conclusion with non-randomized data in the smoking-lung cancer debate.
3. p-values require subjective input from the producer of the data rather than from the consumer of the data.

H. Problems Interpreting and Acting on "Positive" Findings

1. With a large enough sample, a trivial effect can cause an impressively small p-value (statistical significance ≠ clinical significance).
2. Statisticians and subject matter researchers (especially the latter) sought a "seal of approval" for their research by naming a cutoff on what should be considered "statistically significant", and a cutoff of p=0.05 is most commonly used.  Any time there is a threshold there is a motive to game the system, and gaming (p-hacking) is rampant.  Hypotheses are exchanged if the original H₀ is not rejected, subjects are excluded, and because statistical analysis plans are not pre-specified as required in clinical trials and regulatory activities, researchers and their all-too-accommodating statisticians play with the analysis until something "significant" emerges.
3. When the p-value is small, researchers act as though the point estimate of the effect is a population value.
4. When the p-value is small, researchers believe that their conceptual framework has been validated.  

I. Problems Interpreting and Acting on "Negative" Findings

1. Because of B2, large p-values are uninformative and do not assist the researcher in decision making (Fisher said that a large p-value means "get more data").