# J. Berger

## The Statistics Debate (NISS) in Transcript Form

I constructed, together with Jean Miller, a transcript from the October 15 Statistics Debate (with me, J. Berger and D. Trafimow and moderator D. Jeske), sponsored by NISS. It’s so much easier to access the material this way rather than listening to it on the video. Using this link, you can see the words and hear the video at the same time, as well as pause and jump around. Below, I’ve pasted our responses to Question #1. Have fun and please share your comments.

Dan Jeske: [QUESTION 1] Given the issues surrounding the misuses and abuse of p values, do you think they should continue to be used or not? Why or why not?

Deborah Mayo  03:46

Thank you so much. And thank you for inviting me, I’m very pleased to be here. Yes, I say we should continue to use p values and statistical significance tests. Uses of p values are really just a piece in a rich set of tools intended to assess and control the probabilities of misleading interpretations of data, i.e., error probabilities. They’re the first line of defense against being fooled by randomness as Yoav Benjamini puts it. If even larger, or more extreme effects than you observed are frequently brought about by chance variability alone, i.e., p value not small, clearly you don’t have evidence of incompatibility with the mere chance hypothesis. It’s very straightforward reasoning. Even those who criticize p values you’ll notice will employ them, at least if they care to check their assumptions of their models. And this includes well known Bayesian such as George Box, Andrew Gelman, and Jim Berger. Critics of p values often allege it’s too easy to obtain small p values. But notice the whole replication crisis is about how difficult it is to get small p values with preregistered hypotheses. This shows the problem isn’t p values, but those selection effects and data dredging. However, the same data drenched hypothesis can occur in other methods, likelihood ratios, Bayes factors, Bayesian updating, except that now we lose the direct grounds to criticize inferences for flouting error statistical control. The introduction of prior probabilities, which may also be data dependent, offers further researcher flexibility. Those who reject p values are saying we should reject the method because it can be used badly. And that’s a bad argument. We should reject misuses of p values. But there’s a danger of blindly substituting alternative tools that throw out the error control baby with the bad statistics bathwater.

Dan Jeske  05:58

Thank you, Deborah, Jim, would you like to comment on Deborah’s remarks and offer your own?

Jim Berger  06:06

Okay, yes. Well, I certainly agree with much of what Deborah said, after all, a p value is simply a statistic. And it’s an interesting statistic that does have many legitimate uses, when properly calibrated. And Deborah mentioned one such case is model checking where Bayesians freely use some version of p values for model checking. You know, on the other hand, that one interprets this question, should they continue to be used in the same way that they’re used today? Then my, my answer would be somewhat different. I think p values are commonly misinterpreted today, especially when when they’re used to test a sharp null hypothesis. For instance, of a p value of .05, is commonly interpreted as by many is indicating the evidence is 20 to one in favor of the alternative hypothesis. And that just that just isn’t true. You can show for instance, that if I’m testing with a normal mean of zero versus nonzero, the odds of the alternative hypothesis to the null hypothesis can at most be seven to one. And that’s just a probabilistic fact, doesn’t involve priors or anything. It just is, is a is an answer covering all probability. And so that 20 to one cannot be if it’s, if it’s, if a p value of .05 is interpreted as 20 to one, it’s just, it’s just being interpreted wrongly, and the wrong conclusions are being reached. I’m reminded of an interesting paper that was published some time ago now, which was reporting on a survey that was designed to determine whether clinical practitioners understood what a p value was. The results of the survey were published and were not surprising. Most clinical practitioners interpreted the p value as something like a p value of .05 as something like 20 to one odds against the null hypothesis, which again, is incorrect. The fascinating aspect of the paper is that the authors also got it wrong. Deborah pointed out that the p value is the probability under the null hypothesis of the data or something more extreme. The author’s stated that the correct answer was the p value is the probability of the data under the null hypothesis, they forgot the more extreme. So, I love this article, because the scientists who set out to show that their colleagues did not understand the meaning of p values themselves did not understand the meaning of p values.

Dan Jeske  08:42

David?

David Trafimow  08:44

Okay. Yeah, Um, like Deborah and Jim, I’m delighted to be here. Thanks for the invitation. Um and I partly agree with what both Deborah and Jim said, um, it’s certainly true that people misuse p values. So, I agree with that. However, I think p values are more problematic than the other speakers have mentioned. And here’s here’s the problem for me. We keep talking about p values relative to hypotheses, but that’s not really true. P values are relative to hypotheses plus additional assumptions. So, if we call, if we use the term model to describe the null hypothesis, plus additional assumptions, then p values are based on models, not on hypotheses, or only partly on hypotheses. Now, here’s the thing. What are these other assumptions? An example would be random selection from the population, an assumption that is not true in any one of the thousands of papers I’ve read in psychology. And there are other assumptions, a lack of systematic error, linearity, and then we can go on and on, people have even published taxonomies of the assumptions because there are so many of them. See, it’s tantamount to impossible that the model is correct, which means that the model is wrong. And so, what you’re in essence doing then, is you’re using the p value to index evidence against a model that is already known to be wrong. And even the part about indexing evidence is questionable, but I’ll go with it for the moment. But the point is the model was wrong. And so, there’s no point in indexing evidence against it. So given that, I don’t really see that there’s any use for them. There’s, p values don’t tell you how close the model is to being right. P values don’t tell you how valuable the model is. P values pretty much don’t tell you anything that researchers might want to know, unless you misuse them. Anytime you draw a conclusion from a p value, you are guilty of misuse. So, I think the misuse problem is much more subtle than is perhaps obvious at firsthand. So, that’s really all I have to say at the moment.

Dan Jeske  11:28

Thank you. Jim, would you like to follow up?

Jim Berger  11:32

Yes,  so, so,  I certainly agree that that assumptions are often made that are wrong. I won’t say that that’s always the case. I mean, I know many scientific disciplines where I think they do a pretty good job, and work with high energy physicists, and they do a pretty good job of checking their assumptions. Excellent job. And they use p values. It’s something to watch out for. But any statistical analysis, you know, can can run into this problem. If the assumptions are wrong, it’s, it’s going to be wrong.

Dan Jeske  12:09

Deborah…

Deborah Mayo  12:11

Okay. Well, Jim thinks that we should evaluate the p value by looking at the Bayes factor when he does, and he finds that they’re exaggerating, but we really shouldn’t expect agreement on numbers from methods that are evaluating different things. This is like supposing that if we switch from a height to a weight standard, that if we use six feet with the height, we should now require six stone, to use an example from Stephen Senn. On David, I think he’s wrong about the worrying assumptions with using the p value since they have the least assumptions of any other method, which is why people and why even Bayesians will say we need to apply them when we need to test our assumptions. And it’s something that we can do, especially with randomized controlled trials, to get the assumptions to work. The idea that we have to misinterpret p values to have them be relevant, only rests on supposing that we need something other than what the p value provides.

Dan Jeske  13:19

David, would you like to give some final thoughts on this question?

David Trafimow  13:23

Sure. As it is, as far as Jim’s point, and Deborah’s point that we can do things to make the assumptions less wrong. The problem is the model is wrong or it isn’t wrong. Now if the model is close, that doesn’t justify the p value because the p value doesn’t give the closeness of the model. And that’s the, that’s the problem. We’re not we’re not using, for example, a sample mean, to estimate a population mean, in which case, yeah, you wouldn’t expect the sample mean to be exactly right. If it’s close, it’s still useful. The problem is that p values don’t tell you p values aren’t being used to estimate anything. So, if you’re not estimating anything, then you’re stuck with either correct or incorrect, and the answer is always incorrect that, you know, this is especially true in psychology, but I suspect it might even be true in physics. I’m not the physicist that Jim is. So, I can’t say that for sure.

Dan Jeske  14:35

Jim, would you like to offer Final Thoughts?

Jim Berger  14:37

Let me comment on Deborah’s comment about Bayes factors are just a different scale of measurement. My my point was that it seems like people invariably think of p values as something like odds or probability of the null hypothesis, if that’s the way they’re thinking, because that’s the way their minds reason. I believe we should provide them with odds. And so, I try to convert p values into odds or Bayes factors, because I think that’s much more readily understandable by people.

Dan Jeske  15:11

Deborah, you have the final word on this question.

Deborah Mayo  15:13

I do think that we need a proper philosophy of statistics to interpret p values. But I think also that what’s missing in the reject p values movement is a major reason for calling in statistics in science is to give us tools to inquire whether an observed phenomena can be a real effect, or just noise in the data and the P values have intrinsic properties for this task, if used properly, other methods don’t, and to reject them is to jeopardize this important role. As Fisher emphasizes, we need randomized control trials precisely to ensure the validity of statistical significance tests, to reject them because they don’t give us posterior probabilities is illicit. In fact, I think that those claims that we want such posteriors need to show for any way we can actually get them, why.

You can watch the debate at the NISS website or in this blog post.

You can find the complete audio transcript at this LINK: https://otter.ai/u/hFILxCOjz4QnaGLdzYFdIGxzdsg
[There is a play button at the bottom of the page that allows you to start and stop the recording. You can move about in the transcript/recording by using the pause button and moving the cursor to another place in the dialog and then clicking the play button to hear the recording from that point. (The recording is synced to the cursor.)]

Categories: D. Jeske, D. Trafimow, J. Berger, NISS, statistics debate

## Is it impossible to commit Type I errors in statistical significance tests? (i)

.

While immersed in our fast-paced, remote, NISS debate (October 15) with J. Berger and D. Trafimow, I didn’t immediately catch all that was said by my co-debaters (I will shortly post a transcript). We had all opted for no practice. But  looking over the transcript, I was surprised that David Trafimow was indeed saying the answer to the question in my title is yes. Here are some excerpts from his remarks: Continue reading

## The P-Values Debate

National Institute of Statistical Sciences (NISS): The Statistics Debate (Video)

Categories: J. Berger, P-values, statistics debate

## The Statistics Debate! (NISS DEBATE, October 15, Noon – 2 pm ET)

October 15, Noon – 2 pm ET (Website)

### Where do YOU stand?

Given the issues surrounding the misuses and abuse of p-values, do you think p-values should be used? Continue reading

| Tags:

## Frequentstein’s Bride: What’s wrong with using (1 – β)/α as a measure of evidence against the null?

.

ONE YEAR AGO: …and growing more relevant all the time. Rather than leak any of my new book*, I reblog some earlier posts, even if they’re a bit scruffy. This was first blogged here (with a slightly different title). It’s married to posts on “the P-values overstate the evidence against the null fallacy”, such as this, and is wedded to this one on “How to Tell What’s True About Power if You’re Practicing within the Frequentist Tribe”.

In their “Comment: A Simple Alternative to p-values,” (on the ASA P-value document), Benjamin and Berger (2016) recommend researchers report a pre-data Rejection Ratio:

It is the probability of rejection when the alternative hypothesis is true, divided by the probability of rejection when the null hypothesis is true, i.e., the ratio of the power of the experiment to the Type I error of the experiment. The rejection ratio has a straightforward interpretation as quantifying the strength of evidence about the alternative hypothesis relative to the null hypothesis conveyed by the experimental result being statistically significant. (Benjamin and Berger 2016, p. 1)

## High error rates in discussions of error rates: no end in sight

waiting for the other shoe to drop…

“Guides for the Perplexed” in statistics become “Guides to Become Perplexed” when “error probabilities” (in relation to statistical hypotheses tests) are confused with posterior probabilities of hypotheses. Moreover, these posteriors are neither frequentist, subjectivist, nor default. Since this doublespeak is becoming more common in some circles, it seems apt to reblog a post from one year ago (you may wish to check the comments).

Do you ever find yourself holding your breath when reading an exposition of significance tests that’s going swimmingly so far? If you’re a frequentist in exile, you know what I mean. I’m sure others feel this way too. When I came across Jim Frost’s posts on The Minitab Blog, I thought I might actually have located a success story. He does a good job explaining P-values (with charts), the duality between P-values and confidence levels, and even rebuts the latest “test ban” (the “Don’t Ask, Don’t Tell” policy). Mere descriptive reports of observed differences that the editors recommend, Frost shows, are uninterpretable without a corresponding P-value or the equivalent. So far, so good. I have only small quibbles, such as the use of “likelihood” when meaning probability, and various and sundry nitpicky things. But watch how in some places significance levels are defined as the usual error probabilities —indeed in the glossary for the site—while in others it is denied they provide error probabilities. In those other places, error probabilities and error rates shift their meaning to posterior probabilities, based on priors representing the “prevalence” of true null hypotheses.

Begin with one of his kosher posts “Understanding Hypothesis Tests: Significance Levels (Alpha) and P values in Statistics” (blue is Frost): Continue reading

## Frequentstein: What’s wrong with (1 – β)/α as a measure of evidence against the null? (ii)

.

In their “Comment: A Simple Alternative to p-values,” (on the ASA P-value document), Benjamin and Berger (2016) recommend researchers report a pre-data Rejection Ratio:

It is the probability of rejection when the alternative hypothesis is true, divided by the probability of rejection when the null hypothesis is true, i.e., the ratio of the power of the experiment to the Type I error of the experiment. The rejection ratio has a straightforward interpretation as quantifying the strength of evidence about the alternative hypothesis relative to the null hypothesis conveyed by the experimental result being statistically significant. (Benjamin and Berger 2016, p. 1)

The recommendation is much more fully fleshed out in a 2016 paper by Bayarri, Benjamin, Berger, and Sellke (BBBS 2016): Rejection Odds and Rejection Ratios: A Proposal for Statistical Practice in Testing Hypotheses. Their recommendation is:

…that researchers should report the ‘pre-experimental rejection ratio’ when presenting their experimental design and researchers should report the ‘post-experimental rejection ratio’ (or Bayes factor) when presenting their experimental results. (BBBS 2016, p. 3)….

The (pre-experimental) ‘rejection ratio’ Rpre , the ratio of statistical power to significance threshold (i.e., the ratio of the probability of rejecting under H1 and H0 respectively), is shown to capture the strength of evidence in the experiment for Hover H0. (ibid., p. 2)

But in fact it does no such thing! [See my post from the FUSION conference here.] J. Berger, and his co-authors, will tell you the rejection ratio (and a variety of other measures created over the years) are entirely frequentist because they are created out of frequentist error statistical measures. But a creation built on frequentist measures doesn’t mean the resulting animal captures frequentist error statistical reasoning. It might be a kind of Frequentstein monster! [1] Continue reading

## High error rates in discussions of error rates (1/21/16 update)

waiting for the other shoe to drop…

Do you ever find yourself holding your breath when reading an exposition of significance tests that’s going swimmingly so far? If you’re a frequentist in exile, you know what I mean. I’m sure others feel this way too. When I came across Jim Frost’s posts on The Minitab Blog, I thought I might actually have located a success story. He does a good job explaining P-values (with charts), the duality between P-values and confidence levels, and even rebuts the latest “test ban” (the “Don’t Ask, Don’t Tell” policy). Mere descriptive reports of observed differences that the editors recommend, Frost shows, are uninterpretable without a corresponding P-value or the equivalent. So far, so good. I have only small quibbles, such as the use of “likelihood” when meaning probability, and various and sundry nitpicky things. But watch how in some places significance levels are defined as the usual error probabilities and error rates—indeed in the glossary for the site—while in others it is denied they provide error rates. In those other places, error probabilities and error rates shift their meaning to posterior probabilities, based on priors representing the “prevalence” of true null hypotheses. Continue reading

## Are P Values Error Probabilities? or, “It’s the methods, stupid!” (2nd install)

.

Despite the fact that Fisherians and Neyman-Pearsonians alike regard observed significance levels, or P values, as error probabilities, we occasionally hear allegations (typically from those who are neither Fisherian nor N-P theorists) that P values are actually not error probabilities. The denials tend to go hand in hand with allegations that P values exaggerate evidence against a null hypothesis—a problem whose cure invariably invokes measures that are at odds with both Fisherian and N-P tests. The Berger and Sellke (1987) article from a recent post is a good example of this. When leading figures put forward a statement that looks to be straightforwardly statistical, others tend to simply repeat it without inquiring whether the allegation actually mixes in issues of interpretation and statistical philosophy. So I wanted to go back and look at their arguments. I will post this in installments.

1. Some assertions from Fisher, N-P, and Bayesian camps

Here are some assertions from Fisherian, Neyman-Pearsonian and Bayesian camps: (I make no attempt at uniformity in writing the “P-value”, but retain the quotes as written.)

a) From the Fisherian camp (Cox and Hinkley):

For given observations y we calculate t = tobs = t(y), say, and the level of significance pobs by

pobs = Pr(T > tobs; H0).

….Hence pobs is the probability that we would mistakenly declare there to be evidence against H0, were we to regard the data under analysis as being just decisive against H0.” (Cox and Hinkley 1974, 66).

Thus pobs would be the Type I error probability associated with the test.

b) From the Neyman-Pearson N-P camp (Lehmann and Romano):

“[I]t is good practice to determine not only whether the hypothesis is accepted or rejected at the given significance level, but also to determine the smallest significance level…at which the hypothesis would be rejected for the given observation. This number, the so-called p-value gives an idea of how strongly the data contradict the hypothesis. It also enables others to reach a verdict based on the significance level of their choice.” (Lehmann and Romano 2005, 63-4)

Very similar quotations are easily found, and are regarded as uncontroversial—even by Bayesians whose contributions stood at the foot of Berger and Sellke’s argument that P values exaggerate the evidence against the null. Continue reading

Categories: frequentist/Bayesian, J. Berger, P-values, Statistics

## U-Phil: Deconstructions [of J. Berger]: Irony & Bad Faith 3

Memory Lane: 2 years ago:
My efficient Errorstat Blogpeople1 have put forward the following 3 reader-contributed interpretive efforts2 as a result of the “deconstruction” exercise from December 11, (mine, from the earlier blog, is at the end) of what I consider:

“….an especially intriguing remark by Jim Berger that I think bears upon the current mindset (Jim is aware of my efforts):

Too often I see people pretending to be subjectivists, and then using “weakly informative” priors that the objective Bayesian community knows are terrible and will give ridiculous answers; subjectivism is then being used as a shield to hide ignorance. . . . In my own more provocative moments, I claim that the only true subjectivists are the objective Bayesians, because they refuse to use subjectivism as a shield against criticism of sloppy pseudo-Bayesian practice. (Berger 2006, 463)” (From blogpost, Dec. 11, 2011)
_________________________________________________
Andrew Gelman:

The statistics literature is big enough that I assume there really is some bad stuff out there that Berger is reacting to, but I think that when he’s talking about weakly informative priors, Berger is not referring to the work in this area that I like, as I think of weakly informative priors as specifically being designed to give answers that are _not_ “ridiculous.”

Keeping things unridiculous is what regularization’s all about, and one challenge of regularization (as compared to pure subjective priors) is that the answer to the question, What is a good regularizing prior?, will depend on the likelihood.  There’s a lot of interesting theory and practice relating to weakly informative priors for regularization, a lot out there that goes beyond the idea of noninformativity.

To put it another way:  We all know that there’s no such thing as a purely noninformative prior:  any model conveys some information.  But, more and more, I’m coming across applied problems where I wouldn’t want to be noninformative even if I could, problems where some weak prior information regularizes my inferences and keeps them sane and under control. Continue reading

Categories: Gelman, Irony and Bad Faith, J. Berger, Statistics, U-Phil |