Sunday Bayes: A brief history of Bayesian stats

The following discussion is essentially nontechnical; the aim is only to convey a little introductory “feel” for our outlook, purpose, and terminology, and to alert newcomers to common pitfalls of understanding.

Sometimes, in our perplexity, it has seemed to us that there are two basically different kinds of mentality in statistics; those who see the point of Bayesian inference at once, and need no explanation; and those who never see it, however much explanation is given.

Sunday Bayes

The format of this series is short and simple: Every week I will give a quick summary of a paper while sharing a few excerpts that I like. If you’ve read our eight easy steps paper and you’d like to follow along on this extension, I think a pace of one paper per week is a perfect way to ease yourself into the Bayesian sphere.

Bayesian Methods: General Background

The necessity of reasoning as best we can in situations where our information is incomplete is faced by all of us, every waking hour of our lives. (p. 2)

In order to understand Bayesian methods, I think it is essential to have some basic knowledge of their history. This paper by Jaynes (pdf) is an excellent place to start.

[Herodotus] notes that a decision was wise, even though it led to disastrous consequences, if the evidence at hand indicated it as the best one to make; and that a decision was foolish, even though it led to the happiest possible consequences, if it was unreasonable to expect those consequences. (p. 2)

Jaynes traces the history of Bayesian reasoning all the way back to Herodotus in 500BC. Herodotus could hardly be called a Bayesian, but the above quote captures the essence of Bayesian decision theory: take the action that maximizes your expected gain. It may turn out to be the wrong choice in the end, but if your reasoning that leads to your choice is sound then you took the correct course.

After all, our goal is not omniscience, but only to reason as best we can with whatever incomplete information we have. To demand more than this is to demand the impossible; neither Bernoulli’s procedure nor any other that might be put in its place can get something for nothing. (p. 3)

Much of the foundation for Bayesian inference was actually laid down by James Bernoulli, in his work Ars Conjectandi (“the art of conjecture”) in 1713. Bernoulli was the first to really invent a rational way of specifying a state of incomplete information. He put forth the idea that one can enumerate all “equally possible” cases N, and then count the number of cases for which some event A can occur. Then the probability of A, call it p(A), is just M/N, or the number of cases on which A can occur (M) to the total number of cases (N).

Jaynes gives only a passing mention to Bayes, noting his work “had little if any direct influence on the later development of probability theory” (p. 5). Laplace, Jeffreys, Cox, and Shannon all get a thorough discussion, and there is a lot of interesting material in those sections.

Despite the name, Bayes’ theorem was really formulated by Laplace. By all accounts, we should all be Laplacians right now.

The basic theorem appears today as almost trivially simple; yet it is by far the most important principle underlying scientific inference. (p. 5)

Laplace used Bayes’ theorem to estimate the mass of Saturn, and, by the best estimates when Jaynes was writing, his estimate was correct within .63%. That is very impressive for work done in the 18th century!

This strange history is only one of the reasons why, today [speaking in 1984], we Bayesians need to take the greatest pains to explain our rationale, as I am trying to do here. It is not that it is technically complicated; it is the way we have all been thinking intuitively from childhood. It is just so different from what we were all taught in formal courses on “orthodox” probability theory, which paralyze the mind into an inability to see a distinction between probability and frequency. Students who come to us free of that impediment have no difficulty in understanding our rationale, and are incredulous to anyone that could fail to understand it. (p. 7)

The sections on Laplace, Jeffreys, Cox and Shannon are all very good, but I will skip most of them because I think the most interesting and illuminating section of this paper is “Communication Difficulties” beginning on page 10.

Our background remarks would be incomplete without taking note of a serious disease that has afflicted probability theory for 200 years. There is a long history of confusion and controversy, leading in some cases to a paralytic inability to communicate. (p.10)

Jaynes is concerned in this section with the communication difficulties that Bayesians and frequentists have historically encountered.

[Since the 1930s] there has been a puzzling communication block that has prevented orthodoxians [frequentists] from comprehending Bayesian methods, and Bayesians from comprehending orthodox criticisms of our methods. (p. 10)

On the topic of this disagreement, Jaynes gives a nice quote from L.J. Savage: “there has seldom been such complete disagreement and breakdown of communication since the tower of Babel.” I wrote about one kind of communication breakdown in last week’s Sunday Bayes entry.

So what is the disagreement that Jaynes believes underlies much of the conflict between Bayesians and frequentists?

For decades Bayesians have been accused of “supposing that an unknown parameter is a random variable”; and we have denied hundreds of times with increasing vehemence, that we are making any such assumption. (p. 11)

Jaynes believes the confusion can be made clear by rephrasing the criticism as George Barnard once did.

Barnard complained that Bayesian methods of parameter estimation, which present our conclusions in the form of a posterior distribution, are illogical; for “How could the distribution of a parameter possibly become known from data which were taken with only one value of the parameter actually present?” (p. 11)

Aha, this is a key reformulation! This really illuminates the confusions between frequentists and Bayesians. To show why I’ll give one long quote to finish this Sunday Bayes entry.

Orthodoxians trying to understand Bayesian methods have been caught in a semantic trap by their habitual use of the phrase “distribution of the parameter” when one should have said “distribution of the probability”. Bayesians had supposed this to be merely a figure of speech; i.e., that those who used it did so only out of force of habit, and really knew better. But now it seems that our critics  have been taking that phraseology quite literally all the time.

Therefore, let us belabor still another time what we had previously thought too obvious to mention. In Bayesian parameter estimation, both the prior and posterior distributions represent, not any measurable property of the parameter, but only our own state of knowledge about it. The width of the distribution is not intended to indicate the range of variability of the true values of the parameter, as Barnards terminology had led him to suppose. It indicates the range of values that are consistent with our prior information and data, and which honesty therefore compels us to admit as possible values. What is “distributed” is not the parameter, but the probability. [emphasis added]

Now it appears that, for all these years, those who have seemed immune to all Bayesian explanation have just misunderstood our purpose. All this time, we had thought it clear from our subject-matter context that we are trying to estimate the value that the parameter had at the time the data were taken. [emphasis original] Put more generally, we are trying to draw inferences about what actually did happen in the experiment; not about the things that might have happened but did not. (p. 11)

I think if you really read the section on communication difficulties closely, then you will see that a lot of the conflict between Bayesians and frequentists can be boiled down to deep semantic confusion. We are often just talking past one another, getting ever more frustrated that the other side doesn’t understand our very simple points. Once this is sorted out I think a lot of the problems frequentists see with Bayesian methods will go away.

Video: “A Bayesian Perspective of the Reproducibility Project: Psychology”

I recently gave a talk at the University of Bristol’s Medical Research Council Integrative Epidemiology Unit, titled, “A Bayesian Perspective on the Reproducibility Project: Psychology,” in which I recount the results from our recently published Bayesian reanalysis of the RPP (you can read it in PLOS ONE). In that paper Joachim Vandekerckhove and I reassessed the evidence from the RPP and found that most of the original and replication studies only managed to obtain weak evidence.

I’m very grateful to Marcus Munafo for inviting me out to give this talk. And I’m also grateful to Jim Lumsden for help organizing. We recorded the talk’s audio and synced it to a screencast of my slides, so if you weren’t there you can still hear about it. 🙂

I’ve posted the slides on slideshare, and you can download a copy of the presentation by clicking here. (It says 83 slides, but the last ~30 slides are a technical appendix prepared for the Q&A)

If you think this is interesting and you’d like to learn more about Bayes, you can check out my Understanding Bayes tutorial series and also our paper, “How to become a Bayesian in eight easy steps.”

What does the ASA statement on p-values mean for psychology?

No single index should substitute for scientific reasoning.

— Official ASA statement

TLDR: The American Statistical Association’s officially stance is that p-values are bad measures of evidence. We as psychologists need to recalibrate our intuitions for what constitutes good evidence. See the full statement here. [Link fixed!]

The American Statistical Association just released its long-promised official statement regarding its stance on p-values. If you don’t remember (don’t worry, it was over a year ago), the ASA responded to Basic and Applied Social Psychology’s (BASP) widely publicized p-value ban by saying,

A group of more than two-dozen distinguished statistical professionals is developing an ASA statement on p-values and inference that highlights the issues and competing viewpoints. The ASA encourages the editors of this journal [BASP] and others who might share their concerns to consider what is offered in the ASA statement to appear later this year and not discard the proper and appropriate use of statistical inference.

This development is especially relevant for psychologists, since the p-value is ubiquitous in our literature. I think I have only ever seen a handful of papers without one. Are we using it correctly? What is proper? The ASA is here to set us straight.

The scope of the statement

The statement begins by saying “While the p-value can be a useful statistical measure, it is commonly misused and misinterpreted.” To help clarify how the p-value should be used, the ASA “believes that the scientific community could benefit from a formal statement clarifying several widely agreed upon principles underlying the proper use and interpretation of the p-value.” Their stated goal is to articulate “in non-technical terms a few select principles that could improve the conduct or interpretation of quantitative science, according to widespread consensus in the statistical community.”

So first things first: what is a p-value?

The ASA gives the following definition for a p-value:

a p-value is the probability under a specified statistical model that a statistical summary of the data (for example, the sample mean difference between two compared groups) would be equal to or more extreme than its observed value.

So the p-value is a probability statement about the observed data, and data more extreme than those observed, given an underlying statistical model (e.g., a null hypothesis) is true. How can we use this probability measure?

Six principles for using p-values

The basic gist of the statement is this: p-values can be used as a measure of the misfit between the data with a model (e.g., a null hypothesis), but that measure of misfit does not tell us the probability that the null hypothesis is true (as we all hopefully know by now). It does not tell us what action we should take — submit to a big name journal, abandon/continue a research line, implement an intervention, etc. It does not tell us how big or important the effect we’re studying is. And most importantly (in my opinion), it does not give us a meaningful measure of evidence regarding a model or hypothesis.

Here are the principles:

1. P-values can indicate how incompatible the data are with a specified statistical model.
2. P-values do not measure the probability that the studied hypothesis is true, or the probability that the data were produced by random chance alone.
3. Scientific conclusions and business or policy decisions should not be based only on whether a p-value passes a specific threshold.
4. Proper inference requires full reporting and transparency.
5. A p-value, or statistical significance, does not measure the size of an effect or the importance of a result.
6. By itself, a p-value does not provide a good measure of evidence regarding a model or hypothesis.

In the paper each principle is followed by a paragraph of detailed exposition. I recommend you take a look at the full statement.

So what does this mean for psychologists?

The ASA gives many explicit recommendations and it is worth reading their full (short!) report. I think the most important principle is principle 6. Psychologists mainly use p-values as a measure of the evidence we have obtained against the null hypothesis. You run your study, check the p-value, if p is below .05 then you have “significant” evidence against the null hypothesis, and then you feel justified in doubting it and consequently having confidence in your preferred substantive hypothesis.

The ASA tells us this is not good practice. Taking a p-value as strong evidence just because it is below .05 is actually misleading; the ASA specifically says “a p-value near 0.05 taken by itself offers only weak evidence against the null hypothesis.” I recently discussed a paper on this blog (Berger & Delampady, 1987 [pdf]) that showed exactly this: A p-value near .05 can only achieve a maximum Bayes factor of ~2 with most acceptable priors, which is a very weak level of evidence — and usually it is much weaker still.

The bottom line is this: We need to adjust our intuitions about what constitutes adequate evidence. Joachim Vandekerckhove and I recently concluded that one big reason effects “failed to replicate” in the Reproducibility Project: Psychology is that the evidence for their existence was unacceptably weak to begin with. When we properly evaluate the evidence from the original studies (even before taking publication bias into account) we see there was little reason to believe the effects ever existed in the first place. “Failed” replications are a natural consequence of our current low standards of evidence.

There are many (many, many) papers in the statistics literature showing that p-values overstate the evidence against the null hypothesis; now the ASA have officially taken this stance as well.

Choice quotes

Below I include some quotations think are most relevant to practicing psychologists.

Researchers should recognize that a p-value without context or other evidence provides limited information. For example, a p-value near 0.05 taken by itself offers only weak evidence against the null hypothesis. Likewise, a relatively large p-value does not imply evidence in favor of the null hypothesis; many other hypotheses may be equally or more consistent with the observed data. For these reasons, data analysis should not end with the calculation of a p-value when other approaches are appropriate and feasible.

In view of the prevalent misuses of and misconceptions concerning p-values, some statisticians prefer to supplement or even replace p-values with other approaches. These include methods that emphasize estimation over testing, such as confidence, credibility, or prediction intervals; Bayesian methods; alternative measures of evidence, such as likelihood ratios or Bayes Factors; and other approaches such as decision-theoretic modeling and false discovery rates

The 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.

Whenever a researcher chooses what to present based on statistical results, valid interpretation of those results is severely compromised if the reader is not informed of the choice and its basis. Researchers should disclose the number of hypotheses explored during the study, all data collection decisions, all statistical analyses conducted and all p-values computed. Valid scientific conclusions based on p-values and related statistics cannot be drawn without at least knowing how many and which analyses were conducted, and how those analyses (including p-values) were selected for reporting.

Statistical significance is not equivalent to scientific, human, or economic significance. Smaller p-values do not necessarily imply the presence of larger or more important effects, and larger p-values do not imply a lack of importance or even lack of effect.

Sunday Bayes: Optional stopping is no problem for Bayesians

Optional stopping does not affect the interpretation of posterior odds. Even with optional stopping, a researcher can interpret the posterior odds as updated beliefs about hypotheses in light of data.

Sunday Bayes

The format of this series is short and simple: Every week I will give a quick summary of a paper while sharing a few excerpts that I like. If you’ve read our and you’d like to follow along on this extension, I think a pace of one paper per week is a perfect way to ease yourself into the Bayesian sphere.

Optional stopping: No problem for Bayesians

Bayesian analysts use probability to express a degree of belief. For a flipped coin, a probability of 3/4 means that the analyst believes it is three times more likely that the coin will land heads than tails. Such a conceptualization is very convenient in science, where researchers hold beliefs about the plausibility of theories, hypotheses, and models that may be updated as new data become available. (p. 302)

It is becoming increasingly common to evaluate statistical procedures by way of simulation. Instead of doing formal analyses, we can use flexible simulations to tune many different parameters and immediately see the effect it has on the behavior of a procedure.

Simulation results have a tangible, experimental feel; moreover, if something is true mathematically, we should be able to see it in simulation as well. (p. 303)

But this brings with it a danger that the simulations performed might be doing the wrong thing, and unless we have a good grasp of the theoretical background of what is being simulated we can easily be misled. In this paper, Rouder (pdf) shows that common intuitions we have for evaluating simulations of frequentist statistics often do not translate to simulations of Bayesian statistics.

The critical element addressed here is whether optional stopping is problematic for Bayesians. My  argument is that both sets of authors use the wrong criteria or lens to draw their conclusions. They evaluate and interpret Bayesian statistics as if they were frequentist statistics. The more germane question is whether Bayesian statistics are interpretable as Bayesian statistics even if data are collected under optional stopping. (p. 302)

When we evaluate a frequentist procedure via simulation, it is common to set a parameter to a certain value and evaluate the number of times certain outcomes occur. For example, we can set the difference between two group means to zero, simulate a bunch of p values, and see how many fall below .05. Then we can set the difference to some nonzero number, simulate a bunch of p values, and again see how many are below .05. The first gives you the type-1 error rate for the procedure, and the second gives you the statistical power. This is appropriate for frequentist procedures because the probabilities calculated are always conditional on one or the other hypothesis being true.

One might be tempted to evaluate Bayes factors in the same way; that is, set the difference between two groups to zero and see how many BFs are above some threshold, and then set the difference to something nonzero and see how many BFs are again above some threshold.

The critical error … is studying Bayesian updating conditional on some hypothetical truth rather than conditional on data. This error is easy to make because it is what we have been taught and grown familiar with in our frequentist training. (p. 308)

Evaluating simulations of Bayes factors in this way is incorrect. Bayes factors (and posterior odds) are conditional on only the data observed. In other words, the appropriate evaluation is: “Given that I have observed this data (i.e., BF = x), what is the probability the BF was generated by H1 vs H0?”

Rouder visualizes this as follows. Flip a coin to choose the true hypothesis, then simulate a Bayes factor, and repeat these two steps many many times. At the end of the simulation, whenever BF=x is observed, check and see how many of these came from one model vs the other. The simulation shows that in this scenario if we look at all the times BF=3 is observed, there will be 3 BFs from the true model to every 1 BF from the false model. Since the prior odds are 1 to 1, the posterior odds equals the Bayes factor.

You can see in the figure above (taken from Rouder’s figure 2), the distribution of Bayes factors observed when the null is true (purple, projected downwards) vs when the alternative is true (pink, projected upwards). Remember, the true hypothesis was chosen by coin flip. You can clearly see that when a BF of 3 to 1 in favor of the null is observed, the purple column is three times bigger than the pink column (shown with the arrows).

Below (taken from Rouder’s figure 2) you see what happens when one employs optional stopping (e.g., flip a coin to pick underlying true model, then sample until BF favors one model to another by at least 10 or you reach a maximum n). The distribution of Bayes factors generated by each model becomes highly skewed, which is often taken as evidence that conclusions drawn from Bayes factors depend on the stopping rule. The incorrect interpretation would be: Given the null is true, the number of times I find BF=x in favor of the alternative (i.e., in favor of the wrong model) has gone up, therefore the BF is sensitive to optional stopping. This is incorrect because it conditions on one model being true and checks the number of times a BF is observed, rather than conditioning on the observed BF and checking how often it came from H0 vs. H1.

Look again at what matters: What is the ratio of observed BFs that come from H1 vs. H0 for a given BF? No matter what stopping rule is used, the answer is always the same: If the true hypothesis is chosen by a coin flip, and a BF of 10 in favor of the alternative is observed, there will be 10 times as many observed BFs in the alternative column (pink) than in the null column (purple).

In Rouder’s simulations he always used prior odds of 1 to 1, because then the posterior odds equal the Bayes factor. If one were to change the prior odds then the Bayes factor would no longer equal the posterior odds, and the shape of the distribution would again change; but importantly, while the absolute number of Bayes factors that end up in each bin would change, but the ratios of each pink column to purple column would not. No matter what stopping rule you use, the conclusions we draw from Bayes factors and posterior odds are unaffected by the stopping rule.

Feel free to employ any stopping rule you wish.

This result was recently shown again by Deng, Lu, and Chen in a paper posted to arXiv (pdf link) using similar simulations, and they go further in that they prove the theorem.

A few choice quotes

Page 308:

Optional-stopping protocols may be hybrids where sampling occurs until the Bayes factor reaches a certain level or a certain number of samples is reached. Such an approach strikes me as justifiable and reasonable, perhaps with the caveat that such protocols be made explicit before data collection. The benefit of this approach is that more resources may be devoted to more ambiguous experiments than to clear ones.

Page 308:

The critical error … is studying Bayesian updating conditional on some hypothetical truth rather than conditional on data. This error is easy to make because it iswhat we have been taught and grown familiar with in our frequentist training. In my opinion, the key to understanding Bayesian analysis is to focus on the degree of belief for considered models, which need not and should not be calibrated relative to some hypothetical truth.

Page 306-307:

When we update relative beliefs about two models, we make an implicit assumption that they are worthy of our consideration. Under this assumption, the beliefs may be updated regardless of the stopping rule. In this case, the models are dramatically wrong, so much so that the posterior odds contain no useful information whatsoever. Perhaps the more important insight is not that optional stopping is undesirable, but that the meaningfulness of posterior odds is a function of the usefulness of the models being compared.

Sunday Bayes: Testing precise hypotheses

First and foremost, when testing precise hypotheses, formal use of P-values should be abandoned. Almost anything will give a better indication of the evidence provided by the data against Ho.

Sunday Bayes series intro:

After the great response to the eight easy steps paper we posted, I started a recurring series, where each week I highlight one of the papers that we included in the appendix of the paper. The format is short and simple: I will give a quick summary of the paper while sharing a few excerpts that I like. If you’ve read our eight easy steps paper and you’d like to follow along on this extension, I think a pace of one paper per week is a perfect way to ease yourself into the Bayesian sphere. At the end of the post I will list a few suggestions for the next entry, so vote in the comments or on twitter (@alxetz) for which one you’d like next. This paper was voted to be the next in the series.

(I changed the series name to Sunday Bayes, since I’ll be posting these on every Sunday.)

Testing precise hypotheses

This would indicate that say, claiming that a P-value of .05 is significant evidence against a precise hypothesis is sheer folly; the actual Bayes factor may well be near 1, and the posterior probability of Ho near 1/2 (p. 326)

Berger and Delampady (pdf link) review the background and standard practice for testing point null hypotheses (i.e., “precise hypotheses”). The paper came out nearly 30 years ago, so some parts of the discussion may not be as relevant these days, but it’s still a good paper.

They start by reviewing the basic measures of evidence — p-values, Bayes factors, posterior probabilities — before turning to an example. Rereading it, I remember why we gave this paper one of the highest difficulty ratings in the eight steps paper. There is a lot of technical discussion in this paper, but luckily I think most of the technical bits can be skipped in lieu of reading their commentary.

One of the main points of this paper is to investigate precisely when it is appropriate to approximate a small interval null hypothesis by using a point null hypothesis. They conclude, that most of the time, the error of approximation for Bayes factors will be small (<10%),

these numbers suggest that the point null approximation to Ho will be reasonable so long as [the width of the null interval] is one-half a [standard error] in width or smaller. (p. 322)

A secondary point of this paper is to refute the claim that classical answers will typically agree with some “objective” Bayesian analyses. Their conclusion is that such a claim

is simply not the case in the testing of precise hypotheses. This is indicated in Table 1 where, for instance, P(Ho | x) [NB: the posterior probability of the null] is from 5 to 50 times larger than the P-value. (p. 318)

They also review some lower bounds on the amount of Bayesian evidence that corresponds to significant p-values. They sum up their results thusly,

The message is simple: common interpretation of P-values, in terms of evidence against precise [null] hypotheses, are faulty (p. 323)

and

the weighted likelihood of H1 is at most [2.5] times that of Ho. A likelihood ratio [NB: Bayes factor] of [2.5] is not particularly strong evidence, particularly when it is [an upper] bound. However, it is customary in practice to view [p] = .05 as strong evidence against Ho. A P-value of [p] = .01, often considered very strong evidence against Ho, corresponds to [BF] = .1227, indicating that H1 is at most 8 times as likely as Ho. The message is simple: common interpretation of P-values, in terms of evidence against precise [null] hypotheses, are faulty (p. 323)

A few choice quotes

Page 319:

[A common opinion is that if] θ0 [NB: a point null] is not in [a confidence interval] it can be rejected, and looking at the set will provide a good indication as to the actual magnitude of the difference between θ and θ0. This opinion is wrong, because it ignores the supposed special nature of θo. A point can be outside a 95% confidence set, yet not be so strongly contraindicated by the data. Only by calculating a Bayes factor … can one judge how well the data supports a distinguished point θ0.

Page 327:

Of course, every statistician must judge for himself or herself how often precise hypotheses actually occur in practice. At the very least, however, we would argue that all types of tests should be able to be properly analyzed by statistics

Page 327 (emphasis original, since that text is a subheading):

[It is commonly argued that] The P-Value Is Just a Data Summary, Which We Can Learn To Properly Calibrate … One can argue that, through experience, one can learn how to interpret P-values. … But if the interpretation depends on Ho, the sample size, the density and the stopping rule, all in crucial ways, it becomes ridiculous to argue that we can intuitively learn to properly calibrate P-values.

page 328:

we would urge reporting both the Bayes factor, B, against [H0] and a confidence or credible region, C. The Bayes factor communicates the evidence in the data against [H0], and C indicates the magnitude of the possible discrepancy.

Page 328:

Without explicit alternatives, however, no Bayes factor or posterior probability could be calculated. Thus, the argument goes, one has no recourse but to use the P-value. A number of Bayesian responses to this argument have been raised … here we concentrate on responding in terms of the discussion in this paper. If, indeed, it is the case that P-values for precise hypotheses essentially always drastically overstate the actual evidence against Ho when the alternatives are known, how can one argue that no problem exists when the alternatives are not known?

Vote for the next entry:

1. Edwards, Lindman, and Savage (1963) — Bayesian Statistical Inference for Psychological Research (pdf)
2. Rouder (2014) — Optional Stopping: No Problem for Bayesians (pdf)
3. Gallistel (2009) — The Importance of Proving the Null (pdf)
4. Lindley (2000) — The philosophy of statistics (pdf)