The difference between Bayesian and frequentist inference in a nutshell: With Bayes you start with a prior distribution for θ and given your data make an inference about the θdriven process generating your data (whatever that process happened to be), to quantify evidence for every possible value of θ. With frequentism, you make assumptions about the process that generated your data and infinitely many replications of them, and try to build evidence for what θ is not. 

Frequentism is about the data generating process. Bayes is about the θ generating process.  
Any frequentist criticizing the Bayesian paradigm for requiring one to choose a prior distribution must recognize that she has a possibly more daunting task: to completely specify the experimental design, sampling scheme, and data generating process that were actually used and would be infinitely replicated to allow pvalues and confidence limits to be computed.  
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 

Reject a specific null, and then argue for an arbitrary alternative. It’s pretty remarkable that so few people see how absurd this procedure is. – JP de Ruiter 
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 pvalues 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 problemsolving 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 pvalue of 0.04 and the trial was labeled completely “negative” which seemed problematic to me. [Note: the pvalue was twosided 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 pvalue 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 coprimary endpoint, the secondary endpoints, cosecondary endpoints, etc. This was all because of their paying attention to alphaspending. 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 noninferiority 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(noninferiority), 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 pvalue is P(data in general are less extreme than that observed if H_{0} 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 pvalue 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 k1 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., 2group 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. Jeffrey has an excellent web site.
Several readers have asked me how I could believe all this and publish a frequentistbased 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 modelbuilding 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 subjectmatterguided model specification. The section in the book about specification of interaction terms is perhaps the best example. When I teach the fullsemester 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:
 Teaching clinical trialists to embrace Bayes when they already do in spirit but not operationally. Unlearning things is much more difficult than learning things.
 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.
 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.
 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 and McElreath’s it’s getting to be easier to be Bayesian each day. For a longer list of suggested articles and books recommended for those without advanced statistics background see this. See also Richard McElreath’s online lectures and trialdesign.org. The R brms package, which uses Stan, makes a large class of regression models even more accessible. A large number of R scripts illustrating Bayesian analysis are here.
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 nonstatisticians fared a bit worse). Some of their key findings are as follows.
 When a pvalue is present, (primarily frequentist) statisticians confuse population vs. sample, especially if the pvalue 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.
 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 pvalue 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.
 In previous studies by the authors, they found that “applied researchers presented with not only a pvalue 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 recipelike 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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