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An argument that assumes the very thing that was to have been argued for is guilty of begging the question; signing on to an argument whose conclusion you favor even though you cannot defend its premises is to argue unsoundly, and in bad faith. When a whirlpool of “reforms” subliminally alter the nature and goals of a method, falling into these sins can be quite inadvertent. Start with a simple point on defining the power of a statistical test. Continue reading
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An argument that assumes the very thing that was to have been argued for is guilty of begging the question; signing on to an argument whose conclusion you favor even though you cannot defend its premises is to argue unsoundly, and in bad faith. When a whirlpool of “reforms” subliminally alter the nature and goals of a method, falling into these sins can be quite inadvertent. Start with a simple point on defining the power of a statistical test.
I. Redefine Power?
Given that power is one of the most confused concepts from Neyman-Pearson (N-P) frequentist testing, it’s troubling that in “Redefine Statistical Significance”, power gets redefined too. “Power,” we’re told, is a Bayes Factor BF “obtained by defining H1 as putting ½ probability on μ = ± m for the value of m that gives 75% power for the test of size α = 0.05. This H1 represents an effect size typical of that which is implicitly assumed by researchers during experimental design.” (material under Figure 1). Continue reading
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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)
Slides from my March 17 presentation on “Severe Testing: The Key to Error Correction” given at the Boston Colloquium for Philosophy of Science Alfred I.Taub forum on “Understanding Reproducibility and Error Correction in Science.”
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The allegation that P-values overstate the evidence against the null hypothesis continues to be taken as gospel in discussions of significance tests. All such discussions, however, assume a notion of “evidence” that’s at odds with significance tests–generally Bayesian probabilities of the sort used in Jeffrey’s-Lindley disagreement (default or “I’m selecting from an urn of nulls” variety). Szucs and Ioannidis (in a draft of a 2016 paper) claim “it can be shown formally that the definition of the p value does exaggerate the evidence against H0” (p. 15) and they reference the paper I discuss below: Berger and Sellke (1987). It’s not that a single small P-value provides good evidence of a discrepancy (even assuming the model, and no biasing selection effects); Fisher and others warned against over-interpreting an “isolated” small P-value long ago. But the formulation of the “P-values overstate the evidence” meme introduces brand new misinterpretations into an already confused literature! The following are snippets from some earlier posts–mostly this one–and also includes some additions from my new book (forthcoming).
1. What you should ask…
When you hear the familiar refrain, “We all know that P-values overstate the evidence against the null hypothesis”, what you should ask is:
“What do you mean by overstating the evidence against a hypothesis?”
One honest answer is: Continue reading
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I came across a paper, “Tests of Statistical Significance Made Sound,” by Brian Haig, a psychology professor at the University of Canterbury, New Zealand. It hits most of the high notes regarding statistical significance tests, their history & philosophy and, refreshingly, is in the error statistical spirit! I’m pasting excerpts from his discussion of “The Error-Statistical Perspective”starting on p.7.[1]
The Error-Statistical Perspective
An important part of scientific research involves processes of detecting, correcting, and controlling for error, and mathematical statistics is one branch of methodology that helps scientists do this. In recognition of this fact, the philosopher of statistics and science, Deborah Mayo (e.g., Mayo, 1996), in collaboration with the econometrician, Aris Spanos (e.g., Mayo & Spanos, 2010, 2011), has systematically developed, and argued in favor of, an error-statistical philosophy for understanding experimental reasoning in science. Importantly, this philosophy permits, indeed encourages, the local use of ToSS, among other methods, to manage error. Continue reading
I resume my comments on the contributions to our symposium on Philosophy of Statistics at the Philosophy of Science Association. My earlier comment was on Gerd Gigerenzer’s talk. I move on to Clark Glymour’s “Exploratory Research Is More Reliable Than Confirmatory Research.” His complete slides are after my comments.
GLYMOUR’S ARGUMENT (in a nutshell):
“The anti-exploration argument has everything backwards,” says Glymour (slide #11). While John Ioannidis maintains that “Research findings are more likely true in confirmatory designs,” the opposite is so, according to Glymour. (Ioannidis 2005, Glymour’s slide #6). Why? To answer this he describes an exploratory research account for causal search that he has been developing:
(slide #5)
What’s confirmatory research for Glymour? It’s moving directly from rejecting a null hypothesis with a low P-value to inferring a causal claim. Continue reading
The allegation that P-values overstate the evidence against the null hypothesis continues to be taken as gospel in discussions of significance tests. All such discussions, however, assume a notion of “evidence” that’s at odds with significance tests–generally likelihood ratios, or Bayesian posterior probabilities (conventional or of the “I’m selecting hypotheses from an urn of nulls” variety). I’m reblogging the bulk of an earlier post as background for a new post to appear tomorrow. It’s not that a single small P-value provides good evidence of a discrepancy (even assuming the model, and no biasing selection effects); Fisher and others warned against over-interpreting an “isolated” small P-value long ago. The problem is that the current formulation of the “P-values overstate the evidence” meme is attached to a sleight of hand (on meanings) that is introducing brand new misinterpretations into an already confused literature!
1. What you should ask…
When you hear the familiar refrain, “We all know that P-values overstate the evidence against the null hypothesis”, denying the P-value aptly measures evidence, what you should ask is:
“What do you mean by overstating the evidence against a hypothesis?”
One honest answer is:
“What I mean is that when I put a lump of prior probability π0 > 1/2 on a point null H0 (or a very small interval around it), the P-value is smaller than my Bayesian posterior probability on H0.”
Your reply might then be: (a) P-values are not intended as posteriors in H0 and (b) P-values can be used to determine whether there is evidence of inconsistency with a null hypothesis at various levels, and to distinguish how well or poorly tested claims are–depending on the type of question asked. A report on the discrepancies “poorly” warranted is what controls any overstatements about discrepancies indicated.
You might toss in the query: Why do you assume that “the” correct measure of evidence (for scrutinizing the P-value) is via the Bayesian posterior?
If you wanted to go even further you might rightly ask: And by the way, what warrants your lump of prior to the null? (See Section 3. A Dialogue.) Continue reading
Scientist sees squirrel
Evolutionary ecologist, Stephen Heard (Scientist Sees Squirrel) linked to my blog yesterday. Heard’s post asks: “Why do we make statistics so hard for our students?” I recently blogged Barnard who declared “We need more complexity” in statistical education. I agree with both: after all, Barnard also called for stressing the overarching reasoning for given methods, and that’s in sync with Heard. Here are some excerpts from Heard’s (Oct 6, 2015) post. I follow with some remarks.
If you’re like me, you’re continually frustrated by the fact that undergraduate students struggle to understand statistics. Actually, that’s putting it mildly: a large fraction of undergraduates simply refuse to understand statistics; mention a requirement for statistical data analysis in your course and you’ll get eye-rolling, groans, or (if it’s early enough in the semester) a rash of course-dropping.
This bothers me, because we can’t do inference in science without statistics*. Why are students so unreceptive to something so important? In unguarded moments, I’ve blamed it on the students themselves for having decided, a priori and in a self-fulfilling prophecy, that statistics is math, and they can’t do math. I’ve blamed it on high-school math teachers for making math dull. I’ve blamed it on high-school guidance counselors for telling students that if they don’t like math, they should become biology majors. I’ve blamed it on parents for allowing their kids to dislike math. I’ve even blamed it on the boogie**. Continue reading
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A classic fallacy of rejection is taking a statistically significant result as evidence of a discrepancy from a test (or null) hypothesis larger than is warranted. Standard tests do have resources to combat this fallacy, but you won’t see them in textbook formulations. It’s not new statistical method, but new (and correct) interpretations of existing methods, that are needed. One can begin with a companion to the rule in this recent post:
(1) If POW(T+,µ’) is low, then the statistically significant x is a good indication that µ > µ’.
To have the companion rule also in terms of power, let’s suppose that our result is just statistically significant at a level α. (As soon as the observed difference exceeds the cut-off the rule has to be modified).
Rule (1) was stated in relation to a statistically significant result x (at level α) from a one-sided test T+ of the mean of a Normal distribution with n iid samples, and (for simplicity) known σ: H0: µ ≤ 0 against H1: µ > 0. Here’s the companion:
(2) If POW(T+,µ’) is high, then an α statistically significant x is a good indication that µ < µ’.
(The higher the POW(T+,µ’) is, the better the indication that µ < µ’.)That is, if the test’s power to detect alternative µ’ is high, then the statistically significant x is a good indication (or good evidence) that the discrepancy from null is not as large as µ’ (i.e., there’s good evidence that µ < µ’).
An account of severe testing based on error statistics is always keen to indicate inferences that are not warranted by the data, as well as those that are. Not only might we wish to indicate which discrepancies are poorly warranted, we can give upper bounds to warranted discrepancies by using (2).
POWER: POW(T+,µ’) = POW(Test T+ rejects H0;µ’) = Pr(M > M*; µ’), where M is the sample mean and M* is the cut-off for rejection. (Since it’s continuous, it doesn’t matter if we write > or ≥.)[i]
EXAMPLE. Let σ = 10, n = 100, so (σ/√n) = 1. Test T+ rejects H0 at the .025 level if M > 1.96(1).
Find the power against µ = 2.3. To find Pr(M > 1.96; 2.3), get the standard Normal z = (1.96 – 2.3)/1 = -.84. Find the area to the right of -.84 on the standard Normal curve. It is .8. So POW(T+,2.8) = .8.
For simplicity in what follows, let the cut-off, M*, be 2. Let the observed mean M0 just reach the cut-off 2.
The power against alternatives between the null and the cut-off M* will range from α to .5. Power exceeds .5 only once we consider alternatives greater than M*, for these yield negative z values. Power fact, POW(M* + 1(σ/√n)) = .84.
That is, adding one (σ/ √n) unit to the cut-off M* takes us to an alternative against which the test has power = .84. So, POW(T+, µ = 3) = .84. See this post.
By (2), the (just) significant result x is decent evidence that µ< 3, because if µ ≥ 3, we’d have observed a more statistically significant result, with probability .84. The upper .84 confidence limit is 3. The significant result is much better evidence that µ< 4, the upper .975 confidence limit is 4 (approx.), etc.
Reporting (2) is typically of importance in cases of highly sensitive tests, but I think it should always accompany a rejection to avoid making mountains out of molehills. (However, in my view, (2) should be custom-tailored to the outcome not the cut-off.) In the case of statistical insignificance, (2) is essentially ordinary power analysis. (In that case, the interest may be to avoid making molehills out of mountains.) Power analysis, applied to insignificant results, is especially of interest with low-powered tests. For example, failing to find a statistically significant increase in some risk may at most rule out (substantively) large risk increases. It might not allow ruling out risks of concern. Naturally, what counts as a risk of concern is a context-dependent consideration, often stipulated in regulatory statutes.
NOTES ON HOWLERS: When researchers set a high power to detect µ’, it is not an indication they regard µ’ as plausible, likely, expected, probable or the like. Yet we often hear people say “if statistical testers set .8 power to detect µ = 2.3 (in test T+), they must regard µ = 2.3 as probable in some sense”. No, in no sense. Another thing you might hear is, “when H0: µ ≤ 0 is rejected (at the .025 level), it’s reasonable to infer µ > 2.3″, or “testers are comfortable inferring µ ≥ 2.3”. No, they are not comfortable, nor should you be. Such an inference would be wrong with probability ~.8. Given M = 2 (or 1.96), you need to subtract to get a lower confidence bound, if the confidence level is not to exceed .5 . For example, µ > .5 is a lower confidence bound at confidence level .93.
Rule (2) also provides a way to distinguish values within a 1-α confidence interval (instead of choosing a given confidence level and then reporting CIs in the dichotomous manner that is now typical).
At present, power analysis is only used to interpret negative results–and there it is often called “retrospective power”, which is a fine term, but it’s often defined as what I call shpower). Again, confidence bounds could be, but they are not now, used to this end [iii].
Severity replaces M* in (2) with the actual result, be it significant or insignificant.
Looking at power means looking at the best case (just reaching a significance level) or the worst case (just missing it). This is way too coarse; we need to custom tailor results using the observed data. That’s what severity does, but for this post, I wanted to just illuminate the logic.[ii]
One more thing:
Applying (1) and (2) requires the error probabilities to be actual (approximately correct): Strictly speaking, rules (1) and (2) have a conjunct in their antecedents [iv]: “given the test assumptions are sufficiently well met”. If background knowledge leads you to deny (1) or (2), it indicates you’re denying the reported error probabilities are the actual ones. There’s evidence the test fails an “audit”. That, at any rate, is what I would argue.
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[i] To state power in terms of P-values: POW(µ’) = Pr(P < p*; µ’) where P < p* corresponds to rejecting the null hypothesis at the given level.
[ii] It must be kept in mind that statistical testing inferences are going to be in the form of µ > µ’ =µ0 + δ, or µ ≤ µ’ =µ0 + δ or the like. They are not to point values! (Not even to the point µ =M0.) Take a look at the alternative H1: µ > 0. It is not a point value. Although we are going beyond inferring the existence of some discrepancy, we still retain inferences in the form of inequalities.
[iii] That is, upper confidence bounds are too readily viewed as “plausible” bounds, and as values for which the data provide positive evidence. In fact, as soon as you get to an upper bound at confidence levels of around .6, .7, .8, etc. you actually have evidence µ’ < CI-upper. See this post.
[iv] The “antecedent” of a conditional refers to the statement between the “if” and the “then”.
OTHER RELEVANT POSTS ON POWER
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This was initially posted as slides from our joint Spring 2014 seminar: “Talking Back to the Critics Using Error Statistics”. (You can enlarge them.) Related reading is Mayo and Spanos (2011)
continued…
Since the comments to my previous post are getting too long, I’m reblogging it here to make more room. I say that the issue raised by J. Berger and Sellke (1987) and Casella and R. Berger (1987) concerns evaluating the evidence in relation to a given hypothesis (using error probabilities). Given the information that this hypothesis H* was randomly selected from an urn with 99% true hypothesis, we wouldn’t say this gives a great deal of evidence for the truth of H*, nor suppose that H* had thereby been well-tested. (H* might concern the existence of a standard model-like Higgs.) I think the issues about “science-wise error rates” and long-run performance in dichotomous, diagnostic screening should be taken up separately, but commentators can continue on this, if they wish (perhaps see this related post). Continue reading
0. July 20, 2014: Some of the comments to this post reveal that using the word “fallacy” in my original title might have encouraged running together the current issue with the fallacy of transposing the conditional. Please see a newly added Section 7.
1. What you should ask…
Discussions of P-values in the Higgs discovery invariably recapitulate many of the familiar criticisms of P-values (some “howlers”, some not). When you hear the familiar refrain, “We all know that P-values overstate the evidence against the null hypothesis”, denying the P-value aptly measures evidence, what you should ask is:
“What do you mean by overstating the evidence against a hypothesis?”
Any Jackie Mason fans out there? In connection with our discussion of power,and associated fallacies of rejection*–and since it’s Saturday night–I’m reblogging the following post.
In February [2012], in London, criminologist Katrin H. and I went to see Jackie Mason do his shtick, a one-man show billed as his swan song to England. It was like a repertoire of his “Greatest Hits” without a new or updated joke in the mix. Still, hearing his rants for the nth time was often quite hilarious.
A sample: If you want to eat nothing, eat nouvelle cuisine. Do you know what it means? No food. The smaller the portion the more impressed people are, so long as the food’s got a fancy French name, haute cuisine. An empty plate with sauce!
As one critic wrote, Mason’s jokes “offer a window to a different era,” one whose caricatures and biases one can only hope we’ve moved beyond: But it’s one thing for Jackie Mason to scowl at a seat in the front row and yell to the shocked audience member in his imagination, “These are jokes! They are just jokes!” and another to reprise statistical howlers, which are not jokes, to me. This blog found its reason for being partly as a place to expose, understand, and avoid them. Recall the September 26, 2011 post “Whipping Boys and Witch Hunters”: [i]
Fortunately, philosophers of statistics would surely not reprise decades-old howlers and fallacies. After all, it is the philosopher’s job to clarify and expose the conceptual and logical foibles of others; and even if we do not agree, we would never merely disregard and fail to address the criticisms in published work by other philosophers. Oh wait, ….one of the leading texts repeats the fallacy in their third edition: Continue reading
Experts convene to explore new philosophy of statistics field
Error Statistics Philosophy 