I had a different follow-up planned for my last post but I made a discovery (see title) that caused me to change course. Previously I had made the rather weak point that the SEV function had some odd properties that I didn’t think made sense for inference. Mayo’s response (on Twitter) was: “The primary purpose of the SEV requirement is to block inference as poorly warranted, & rigged exes have bad distance measures.” In this post I’ll argue that the SEV function has properties that I don’t think anyone can claim make sense for inference, and I’ll draw out the consequences of affirming the severity rationale in spite of its possession of these undesirable properties.
Here I’ll examine the SEV function in the context of a modification of Mayo’s “water plant accident” example. For the picturesque details you can follow the link; I’ll stick with the math. The model is normal with unknown mean μ and a standard deviation of 10. Here we are interested in testing H0: μ ≤ 150 vs. H1: μ > 150. Mayo looks at the test based on the mean of 100 samples, which I will call x̅100. My modification is this: we’ll check the mean after collecting 4 samples, x̅4, and reject the null if it’s greater than some threshold; otherwise we’ll collect the remaining 96 samples and test again using x̅100 as our statistic. Which threshold? It hardly matters, but let’s say the threshold for rejection of H0 and cessation of data collection at n = 4 is at x̅4 = 165, three standard errors from the null. (This “spends” 0.00135 of whatever Type I error rate we’re willing to tolerate. In Mayo’s example the Type I error rate is set to 0.022, corresponding to a threshold at x̅100 = 152, two standard errors from the null; in our case, to compensate for the look at n = 4 the threshold at n = 100 increases a very tiny amount — it’s 152.02. Nothing turns on these details.) I’ll also consider what happens when the design is to collect not 96 but 896 additional samples for a total of 900 before the second look.
This is an early stopping design (a.k.a. group sequential design,
adaptive design correction); they’re common in clinical trials where it’s desirable to minimize the number of patients in the event that strong evidence has been observed. Is it a “rigged” example? It sure is. The rigging lies in the fact that in clinical trials the “looks” at the data wouldn’t be as early as this — it generally isn’t worth looking when only 1/25 of the second-look sample size has been observed, much less 1/225. By using this schedule I am deliberately amplifying problems for frequentist inference that already exist in a milder form in more typical trial designs. But we’ve been told that SEV’s primary purpose is to block poorly warranted inferences, and the question we should be asking isn’t “is it rigged?” — it’s whether SEV actually does a reasonable job even in, or perhaps especially in, setups that don’t make a lot of sense. It is, if you will, a severe test of severity reasoning. In any event, I think even a weird design like this ought to be included in the domain of severity reasoning’s application since it’s just twiddling the design parameters of a well-accepted approach.
The postulate on which I’m going to base my argument is this: when early stopping is possible but doesn’t actually occur, the sample mean is consistent for μ and its standard deviation decreases at the usual O(n-½) rate. So, supposing that we haven’t stopped at the first look, the width of the interval in which the value of μ can be bounded ought in all cases to shrink to zero as we consider designs with larger and larger second-look sample size. This is not a likelihood-based notion — this is based on the conditional distribution of the estimator. When I say SEV doesn’t work, I mean that it fails to adhere to this “Precision RespEcts Sample Size” (PRESS) postulate. If you don’t accept this postulate then I invite you to simulate some data. If you still don’t accept this postulate then my argument that SEV doesn’t work may not be convincing to you, but you’ll find that you have to take on board some troubling consequences nevertheless.
(Just to set expectations: the rest of this post is about ten times longer than this introduction; there are equations and plots.)
The SEV function under early stopping
Severity requires a notion of accordance
Let’s recap the severity criteria (Error Statistics, pg 164):
A hypothesis H passes a severe test T with data x0 if,
(S-1) x0 accords with H, (for a suitable notion of accordance) and
(S-2) with very high probability, test T would have produced a result that accords less well with H than x0 does, if H were false or incorrect.
Equivalently, (S-2) can be stated:
(S-2)*: with very low probability, test T would have produced a result that accords as well as or better with H than x0 does, if H were false or incorrect.
In the fixed sample size design, Mayo instantiates the above severity criteria as the SEV function, thus:
in which d(⋅) is a function defining a test statistic and SEV is to be thought of as a function of μ′. (This isn’t quite how she puts it — she generally writes Pr (d(X) < d(x0); μ ≤ μ′) and then writes about finding the lower bound of the probability under μ ≤ μ′. It comes to the same thing.)
The word “suitable” in the phrase “a suitable notion of accordance” is doing a lot of work here. In the fixed sample size design it’s straightforward to translate the notion of “a result that accords less well with μ > μ′ than x0 does” to the event “d(X) < d(x0)”. Accordance is not so easy to nail down when the test statistic could be calculated at more than one possible sample size. Suppose we observe, say, x̅4 = 160 — does this accord more, less, or equally well with larger values of μ than, say, x̅100 = 151.5?
This is where I got stumped when I last looked at early stopping designs; I came up with three fairly obvious candidate notions of accordance but none of them resulted in SEV functions that made sense. This was unacceptable to me because I wanted to be certain of not constructing a straw man — at that time I sought a SEV analysis that was clearly and unassailably correct by error statistical criteria. I would have liked to use the test statistic associated with a uniformly most powerful (UMP) test but I couldn’t find such a test.
(In retrospect looking for a UMP test was pretty silly: the realized sample size and mean are jointly sufficient statistics — you can’t do better than that — and power can always be increased by pushing the early stopping threshold out to infinity, turning your early stopping design into a fixed sample size design. The whole point is to sacrifice power in return for reducing the expected sample size in a way that depends on the true effect size
; hence the name “adaptive design” correction.)
Recently my interest in the question was rekindled by arguments about optional stopping made in Mayo’s new book. I asked Daniël Lakens for some advice on how to handle frequentist inference in such problems and he pointed me to a tutorial paper he wrote that cites Statistical Modelling of Clinical Trials: A Unified Approach by Proschan et al.
In sequential designs the problem of deciding on a notion of accordance arises after the trial has concluded and it’s time to compute the p-value (defined as the probability, under the null hypothesis, of a result as or more extreme than the one actually observed). In Proschan et al. I read that to make “more extreme than the one actually observed” mathematically precise one defines an ordering on the elements of the sample space such that for any two elements one can say which is more extreme (or if they are equally extreme, a circumstance which doesn’t happen in fixed sample size designs). Such an ordering directly specifies a notion of accordance that might be suitable for constructing the SEV function. Proschan et al. offer four possible orderings, and three of them were the three I had thought up previously.
The four orderings are:
- MLE-ordering, which I will denote ≺e (the “e” stands for “estimator”), which calls outcomes equally extreme when the resulting maximum likelihood estimator (MLE) values are numerically equal; in this example the sample means are the MLEs so x̅100 = 154 is simply equivalent to x̅4 = 154;
- B-ordering, the one I didn’t think of and which I won’t describe because in our case it happens to coincide with MLE-ordering;
- z-ordering, ≺z, which calls outcomes equally extreme when they correspond to the same z-score; for example, x̅100 = 154 is equivalent to x̅4 = 170 since they are each four nominal standard errors away from the null;
- stagewise ordering, ≺s, which calls any value of x̅4 more extreme than any value of x̅100 because the larger the value of μ the more likely is early stopping; at a given sample size the test statistic values are ordered as usual.
Proschan et al. strongly recommend stagewise ordering; ironically, I thought of stagewise ordering first and rejected it almost immediately, for reasons that will become clear. They recommend it on three grounds:
- Using other orderings can sometimes result in a p-value that is larger than the design’s Type I error rate even when the null hypothesis has been rejected, but this can never happen using stagewise ordering.
- If the null is rejected at the first look then the p-value is the same as if that result had occurred in a fixed sample size design (I personally don’t see why this is particularly desirable, but okay).
- The other orderings can’t be used with the “alpha-spending function” approach of Lan and DeMets that permits looks at the data that are not planned in advance.
In relation to this last point they write something I find a little odd:
…the p-values for the z-score, B-value, and MLE orderings depend not only on the data observed thus far, but also on future plans. [In a worked example with five looks, even] though we stopped at the third look, we needed to know the boundaries at the fourth and fifth looks. But future look times may be unpredictable. Why should the degree of evidence observed thus far depend on the number and times of looks in the future? This violates the likelihood principle.
The entire approach described in the book violates the version of the likelihood principle I’m familiar with. It’s possible that they mean the thing I know as the sufficiency principle, which states that if two experiments yield the same value of a sufficient statistic then they yield the same evidence about the parameter. But in the sort of group-sequential designs they’re looking at, the MLE and the information fraction (a kind of generalized sample size) at stopping are jointly sufficient and the inference methods they advocate do not depend solely on the realized value of the sufficient statistic, so the sufficiency principle is also violated by their approach. So while I agree that the degree of evidence observed thus far shouldn’t depend on plans for future data collection, I can’t make out what principle they’re citing.
We’ll need two random variables, X̅4 and X̅100:
- they are jointly normally distributed;
- X̅4 has unknown mean μ and standard deviation 5;
- X̅100 has unknown mean μ and standard deviation 1;
- Cov(X̅4, X̅100) = 1.
This completely specifies their joint distribution. Note that the joint distribution is defined on the entire ℝ2 plane; for us the event “no early stopping, n = 100” is identical to the event “X̅4 ≤ 165”. I’ll use x̅n to refer to a generic observed result and, well, I’m not sure what X̅N is exactly but the event “X̅N ≺ x̅n” is the event “an outcome less extreme than the observed result x̅n as defined by whichever ordering ‘≺’ is in use”. This is everything we need to define the candidate SEV functions corresponding to the different orderings; I’ll give them a subscript to indicate which ordering is in use.
It turns out that the candidate SEV functions fall afoul of PRESS when data collection isn’t stopped at the first look and the data at a subsequent look indicates that it “should have”, i.e., that the realized estimate suggests that the parameter value is actually on the “stop” side of the stopping threshold. So let us consider the outcome for which the rejection threshold was not exceeded at the first look at n = 4 and the final result was x̅100 = 170. Is this just a weird result that could effectively never occur even with the most favorable value of μ? No — it turns out that Pr (X̅4 ≤ 165, X̅100 > 170; μ = 171) = 0.086, so while such a result is a bit unusual it’s by no means inconceivable. This probability (with μ tuned to maximize) increases with increasing second-look sample size and asymptotes from below to 0.21.
In stagewise ordering any observed value of x̅100 accords less well with larger values of μ than any value of X̅4 greater than the rejection threshold, so we have
Both of these probabilities are monotonic decreasing in μ so the minimum is achieved when μ = μ′ and we may write
Since the two factors are probabilities, either of them is an upper bound on SEVs; in particular, SEVs ( μ > μ′ ) can never be larger than the probability of no early stopping, Pr (X̅4 ≤ 165; μ′ ).
Figure 1. Under stagewise ordering, lower-bounding inferences (i.e., inferences of the form “μ > μ′ ”) are constrained by the rejection threshold.
Figure 1 shows SEVs ( μ > μ′ ) (solid) along with the probability of no early stopping (dashed). Consider the severity for the inference “μ > 165”. SEVs ( μ > 165) is smaller than its upper bound, 0.5, albeit negligibly so. In the Error Statistics paper at the bottom of page 171 we learn that SEV less than 0.5 is considered poor warrant for an inference, so an error statistician who uses stagewise ordering finds that the severity rationale blocks her from making the lower-bounding inference “μ > 165”. The inference is blocked by the fact that, even supposing μ ≤ 165, there’s appreciable probability that data collection would have stopped early and thereby produced a result that (stagewise-)accords better with “μ > 165” than any value of x̅100 does (compare criterion (S-2)*). Take note: having looked and not stopped, she’s permanently blocked from inferring “μ > 165” irrespective of the second-look sample size of the design. It doesn’t matter if she takes the second look after collecting 100, 900, or 250,000 samples; to hold to stagewise ordering she must give up PRESS.
Proschan et al. note that stagewise ordering has related consequences for confidence interval procedures. In fact, the construction of such intervals is mathematically equivalent to reading the tail area probabilities off the SEVs curve, so stagewise ordering results in a bound on the lower confidence limit, and for equal-tailed intervals and a fixed budget of confidence this implies a bound on the upper confidence limit too. As a result, it’s possible for the MLE to lie outside the confidence interval, although the chances are “microscopic” for trial designs and confidence levels typically used in practice. The fact that the width of the confidence interval can end up being bounded below without respect to the realized sample size with non-negligible probability was not remarked on, likely because the phenomenon is both unusual and relatively mild when the sample sizes are closer together.
Figure 2. Under stagewise ordering, upper-bounding inferences respect realized sample size.
Speaking of interval procedures, we’ve looked at SEVs for lower-bounding inferences and we should do the same for upper-bounding inferences. It turns out that with stagewise ordering we have SEVs ( μ < μ′ ) = 1 – SEVs ( μ > μ′ ). This relationship holds for the sorts of examples Mayo usually discusses (see for example the Error Statistics paper, middle of page 172) and for stagewise ordering but can fail for other orderings. Figure 2 shows SEVs ( μ < μ′ ) for an observed mean of 170 for two designs, one with a second-look sample size of 100 (in blue) and one with a second-look sample size of 900 (in red). The upper bound does converge with increasing sample size, so that’s okay.
How does z-ordering perform? Well, x̅100 = 170 is twenty nominal standard errors from the null, so according to z-ordering it is as extreme as x̅4 = 250 and we have
The minimand in the expression is non-monotonic; I don’t even know if Mayo would allow orderings that lead to non-monotonicity but I have relevant points to make even if she wouldn’t, so let’s proceed.
Figure 3. Under z-ordering, upper-bounding inferences mix first-look and second-look distributions together in a bizarre way.
Figure 3 shows SEVz ( μ > μ′ ) (solid) and the minimand of the SEVz ( μ > μ′ ) expression (dashed). The minimand rises from its local minimum and stays at (effectively) one until μ′ approaches 250, so SEVz ( μ > μ′ ) stays locked to the value of the minimand at the local minimum, 0.913, until the minimand descends below that value near μ′ = 243. As we consider larger and larger second-look sample sizes the value of x̅4 equivalent to an observed mean of 170 at the second-look sample size to goes off to infinity. In the same limit the descent of the minimand close to 170 gets sharper and the limiting value of SEVz ( μ > μ′ ) is 0.841; that is, we always have SEVz ( μ > μ′ ) > 0.841 for all values of μ′ from 170 on out and out and out…
What are we to make of this value, 0.841? Well, the Error Statistics paper characterizes it as “not too bad” close to the bottom of page 171. Returning to the scenario where the second-look sample size is 100, we see that an error statistician who uses z-ordering would be led to affirm that, say, the inference “μ > 200” has a warrant that is at least “not too bad” because there is a high probability that a z-score that accords more with μ ≤ 200 than does the realized z-score would have been observed, supposing μ ≤ 200. This violates PRESS, but I think it’s fair to say that’s the least of its problems.
(Here we have the SEVz function seeming to warrant an inference it shouldn’t, but the definition of the SEV function only draws on criterion (S-2); an error statistician would probably block “μ > 200” due to failure of criterion (S-1). Exactly how that would go is unclear because the Error Statistics paper only shows applications of (S-1) to the null or alternative hypothesis of a test and not to arbitrary directional inferences. It also says that an error statistician could use likelihood to arrive at (S-1); in all, the proper application of criterion (S-1) is quite mysterious.)
But really the point I want to make with this ordering relates to upper bounding inferences, not lower bounding inferences.
To a high degree of accuracy this is just
Never mind that the z-ordering’s value of x̅4 equivalent to x̅100 = 170 doesn’t make sense. The point is that the curvature of the SEVz ( μ < μ′ ) function is determined by the standard error at n = 4. Even if we hypothesize some other ordering that slides the equivalent value of x̅4 down to something more reasonable this will remain true. In fact, let’s do just that.
Figure 4. Under any ordering that treats possible results at the first look and second look as equivalently extreme, the width of intervals between upper-bounding and lower-bounding inferences can end up insensitive to the second-look sample size.
Figure 4 shows possible SEV ( μ < μ′ ) functions for hypothetical orderings that set the equivalent value of x̅4 to 170 (leftmost/highest), 175 (center), and 180 (rightmost/lowest) for both a second-look sample size of 100 (blue) and 900 (red). The overall width of each curve is pretty much the same no matter where we center the curve and, critically, no matter the second-look sample size. All a larger sample size accomplishes is to make the curve in the region around 170 steeper; there will be inferences that, at any level we might consider well-warranted, are insensitive to the second-look sample size of the design.
In Figure 4 the ordering that set the equivalent value of x̅4 to 170 wasn’t actually hypothetical — that’s exactly what MLE-ordering does. SEVe ( μ < μ′ ) doesn’t look too bad, does it? It’s centered around the right place, unlike the stagewise ordering version. Sure, the precision is “wrong” but it’s conservatively wrong, which might be tolerable to someone who doesn’t require PRESS.
Lest anyone be tempted by the seeming acceptability of this result, it must be pointed out that in MLE-ordering it doesn’t matter at which look you observe a particular realized mean — the SEVe function depends only on the value of the observed mean. This can lead to results that illustrate exactly why Proschan et al. recommend an ordering in which the degree of evidence observed at early looks doesn’t depend on details relating to later looks.
Figure 5. Under MLE-ordering it doesn’t matter if you observe x̅4 = 165.7 or x̅100 = 165.7, but the planned second-look sample size does affect the inference even if early stopping occurred.
Figure 5 shows two SEVe ( μ < μ′ ) functions for x̅4 = 165.7, corresponding to two different second-look sample sizes, 100 (blue) and 900 (red). The curvature at values below 0.5 reflect the width of the sampling distribution for the first look but above 0.5 the curvature reflects the smaller width of the sampling distribution for the second look even though the second look hasn’t and won’t take place. An error statistician who holds to MLE-ordering and planned a second-look sample size of 100 would claim that given x̅4 = 165.7, “μ < 168” is a well-warranted inference because there’s a high probability of observing a sample mean larger than 165.7 supposing that μ ≥ 168. If she had instead planned a second-look sample size of 900 then the same would go for the claim “μ < 167”. This isn’t a violation of PRESS per se but I think it’s fair to say that appropriating precision from an unfulfilled plan to look at more data is behavior no one wants from their method of inference.
Conditioning on realized sample size
This early stopping design is somewhat akin to one that was used to level criticisms against Neyman-Pearson testing in years gone by: one of two measurement devices, one low precision and one high precision, is chosen at random and then the measurement is carried out. The specific criticism is that if one calculates error probabilities that take the random selection of measurement devices into account (in statistical jargon the sampling distribution is a mixture model) one ends up with a rejection region that seems inappropriate for either device, being too lenient on the null hypothesis relative to the high precision measurement and too strict on the null hypothesis relative to the low precision measurement. The p-value associated with the mixture has a corresponding affliction. Proponents of hypothesis testing address the criticism by noting that the choice of measurement is “ancillary” — its sampling distribution is free of the parameter of interest — but informative about the precision of the measurement; they argue, reasonably enough, that it’s appropriate to condition on such ancillary information when performing inference. In cases like our early stopping scenario, however, the sample size is not an ancillary random variable —
its dependence on the parameter of interest is what makes adaptive trials adaptive correction — so a straightforward resort to conditioning is not justified.
But you know what? Let’s try conditioning anyway and see what happens. Consider a one-sided lower-bounding confidence procedure in which for a chosen confidence level (1 – α), one seeks the value of μ such that the observed mean is at the the α quantile of its sampling distribution conditional on whether early stopping occurred or not. As we slide the confidence level from 1 to 0 we trace out a function that looks a lot like a candidate SEV ( μ > μ′ ). This is an exact confidence procedure but it doesn’t correspond to any simple notion of accordance over the whole sample space. Is it legitimate to use a notion of accordance (and relevant outcome space) that is sampled at random in a manner that depends on the parameter of interest? I don’t know — Mayo never addresses complicated examples.
By design, the inferences this procedure produces at the second look adhere to PRESS. They aren’t identical to the inferences that would result in a fixed sample size design so perhaps they can also be said to have adjusted the error probabilities to take selection effects into account, a property Mayo considers essential to well-warranted inference. The problem comes when we consider the inferences that result when early stopping does occur and the observed mean is close to the rejection threshold. We’re obliged to use the sampling distribution conditional on the occurrence of early stopping; otherwise the confidence coverage of the procedure taken as a whole is wrong. We find that the resulting inferences are subject to an extreme form of the first problem Proschan et al. noted for orderings other than stagewise: the conditional procedure produces an inference that contradicts the Type I error rate set in the design of the trial.
For example, when x̅4 = 166 the inference “μ > 150” has confidence level Pr (X̅4 < 166 | X̅4 > 165; μ = 150) = 0.49; the p-value for the corresponding test is 0.51. It’s a peculiar sort of contradiction. By using this experimental design we aimed to ensure a Type I error rate no greater than 0.022; the particular rejection threshold that was exceeded has only a 0.00135 Type I error rate associated with it. The result is more than three standard errors from the null! It seems like we ought to be able to claim “μ > 150” with a SEV of at least 0.978. And yet, if the severity rationale is even available on a conditional basis then, given this procedure and result, it blocks the inference: among the cases that reject on the first look there’s appreciable probability of a result that accords better with “μ > 150” than does x̅4 = 166, even supposing μ ≤ 150. I can’t imagine anyone would uphold this line of reasoning, but I admit that all I have here is an argument from incredulity. If anyone can argue convincingly that this or something like it is actually reasonable then I’d have to reconsider, but I think it’s fair to say such an argument would have to go well beyond any argument Mayo herself has made up to this point.
Error-statistical construals of frequentist procedures with multiple looks
I’ve demonstrated that no simple measure of accordance results in a SEV function that follows PRESS in all cases. (I say “simple” because I only looked at the most obvious candidate SEV functions. I’ve thought up some baroque possibilities but I can’t sort out an error-statistical principle that can be applied to uniquely specify a particular choice. I’ve reached the end of both my ability and motivation to steelman the SEV function and no one else has even seen the need, so I’m going forward on the assumption that this is as good at it gets. If someone generates a principled notion of accordance that addresses these problems I can revise my views.) I’ve also shown that simple conditioning on realized sample size, the most straightforward way of constructing a frequentist procedure that follows PRESS, works for second looks but can block the first-look inference for which the test was designed. In the face of this tension between SEV and PRESS, those fully committed to severity reasoning might simply deny that adherence to PRESS is a necessary property of a method of inference. I see two ways one might go about this.
First, one might simply deny that a fully general notion of accordance exists in designs with multiple looks. One might permit the use of stagewise ordering for p-value calculations but forbid calculating post-data error probabilities for hypotheses other than the null, ruling out a SEV function defined on the full parameter space. This will still leave the severity rationale available when considering p-values as in the Error Statistics paper at the top of page 168.
This is the sort of stance that might appeal to someone like Daniël Lakens, who is fully committed to Neyman-Pearson testing and has little use for effect size estimates. From what I understand, in his investigations effect sizes are experiment-bound and aren’t expected to generalize, so he is much more interested in whether any effect at all can be generated and discerned than with the magnitude of the effect. In his tutorial paper on sequential designs he recommends caution regarding effect size estimates, writing
…the observed effect size at the moment the study is stopped could be an overestimation of the true effect size. Although procedures to control for bias have been developed, there is still much discussion about the interpretation of such effect sizes, and studies using non-adaptive designs, followed by a meta-analysis, might be needed if an accurate effect size estimate is paramount.
The unappealing consequence of this stance is that it undermines many defences of frequentist statistics made in Error Statistics paper, at least in the context of designs with multiple looks. In particular, the paper’s counter-arguments to “fallacies” or “errors” in interpreting hypothesis/significance test results (#2, #3, and #6) all rely on the existence of the SEV function; without a suitable notion of accordance, the whole defence is thrown back on the power function as an aid to the interpretation of dichotomous test results. The paper’s claim that when a statistically significant result is found, “[p]ost-data, one can go much further in determining the magnitude γ of discrepancies from the null warranted by the actual data in hand” would no longer hold, and post-data assessment of statistically insignificant results would likewise no longer be available. Our inferences would depend only on whether the test rejected the null or not, to the neglect of most of the information in the data. On this view, observing x̅100 = 170 justifies nothing more than the strong rejection of the null that we can get from the p-value and the inferences we can get from considering the pre-data probability of Type II error.
The staunchest advocates of the severity rationale can avoid undermining these defences by taking the second option: biting the bullet and committing to some fully general notion of accordance even in the multiple look context. At the risk of going out on a limb, I’m going to assume that in light of the my discussion of z-ordering and MLE-ordering and in view of Proschan et al.’s first and third arguments for stagewise ordering (non-contradiction of p-values and Type I error rates, applicability even for unplanned interim looks), their choice would indeed be stagewise ordering. The unappealing consequence of this stance has already been described in mathematical terms; the nickel summary is that when the sheer existence of later observations is contingent on the earlier result they cannot force the SEV function past the worst case consistent with the earlier result. In figurative language we might say that each look at the data that does not trigger the end of data collection acts as a ratchet, constraining the set of possible well-warranted inference in a way that allows free movement in only one direction.
I have to imagine that this is not the first time that a critic of frequentist statistics — perhaps Richard Royall or some other likelihood theorist — has discovered this ratcheting of inferences in sequential trials as it manifests in confidence intervals. I can also see how criticism based on this phenomenon might not be convincing to frequentists who appeal to what the Error Statistics paper calls the “behavioristic rationale… wherein tests are interpreted as tools for deciding “how to behave” in relation to the phenomena under test, and are justified in terms of their ability to ensure low long-run errors.” What’s novel here is that I’ve drawn out the consequences of an account that purports to delineate well-warranted inferences from poorly warranted inferences in the specific case at hand rather than simply ensuring low errors in the long run. The account is supposed to provide a philosophical foundation for frequentist statistical techniques in current use and, what’s more, to be an account of how people actually reason “in the wild”. If you collected 4 samples, observed a sample mean below your rejection threshold of 165, continued by collecting 249,996 more samples, and then observed a sample mean of 170, is this how you would reason?
The stagewise ordering ratchet is bad enough in the context of a single early stopping design, but there is worse to come.
Error and the constriction of experimental knowledge
A pattern of contingent, sequential investigations of an effect is a relatively small part of science, but it’s not a negligible one. Witness this tweet by statistician Zad Chow: “Thought experiment. Pretend several studies on a phenomenon (an intervention) failed to produce a statistically significant effect. You design a new study, intended to have really high power (like 90%). You find no significant effect. Is this support for no difference?” His point relates to the interpretation of statistically insignificant results; my point relates to just how natural it is to imagine studies that wouldn’t even exist had previous studies found different results. If you don’t find some rando’s tweet compelling evidence, consider what the distinguished applied statistician Stephen Senn has to say about power calculations and sample size: set the sample size to control the rate of two errors, Type I error and “the error of failing to develop a (very) interesting treatment further”. Really, the idea that researchers decide which lines of research to pursue in light of past results would ordinarily be too banal to merit notice, but it matters here.
How are frequentist statistical techniques used in science? A stylized account goes something like this: we draw a conceptual border around our Study; inside this border we design the Study to achieve a particular Type I error rate and power function, and when data have been collected we calculate our inferential statistics in isolation of anything outside of the Study. At the end we (hopefully!) publish a paper relating the findings of our Study to the scientific community at large. Other researchers may then survey the literature and make decisions about what they’re going to do on the basis of information that includes the Study — for that matter we almost certainly looked at prior Studies ourselves before conducting our own Study — but it would be infeasible to try to account for how our current choices are contingent on those findings and would have been different had those findings been different. Of course, within the context of the Study itself we had better be prepared to account for data collection that was contingent on interim findings or else our inferences will not survive an error-statistical audit.
After many Studies of an effect have been conducted, how can we synthesize the information in the literature? We employ the techniques of meta-analysis to conduct another Study, naturally. A meta-Study has as sturdy a conceptual border around it as any other Study, and of course it respects the conceptual borders around the Studies that constitute its data — Studies are treated as independent and no attempt is made to account for the possibility that the sheer existence of later Studies might be contingent on the findings of earlier Studies.
For a severity-based account of statistical inference in science to work it is absolutely crucial that the conceptual borders around Studies be enforced and the possibility of contingent existence of later Studies be ignored. If we were to acknowledge it we’d be obliged to compute error probabilities in a sequential fashion to avoid committing the sin of ignoring selection effects. Stagewise ordering would be the only practical choice here as it only requires knowing what has happened and not future plans.
Consider the implications for replication studies: an initial well-conducted (perhaps even pre-registered) study finds a result that’s just barely statistically significant at the conventional 2.5% level (Mayo treats two-sided tests as two one-sided tests). The sample size was set in accordance with Stephen Senn’s advice linked above to have high power to reject the null under “the [effect size] we would not like to miss”, so naturally this result prompts researchers to carry out a larger study that would never have happened had the initial study found no evidence of an interesting effect. The follow-on study has much higher precision and shows a smaller effect than in the initial study; the first has a 95% CI of, say, [0.03, 3.95] and the second a 95% CI of [0.46, 1.24] on the same scale; the “effect size we would not like to miss” is around 3 on this scale. Of course, the later inference is carried out ignoring its own contingent existence; data collection wasn’t stopped after the first study and the data in the subsequent study indicates that it “should have”, so the stagewise ordering ratchet binds and blocks the inference to a smaller effect. Accounting for the sequential relationship between the two investigations yields a 95% CI of [0.66, 3.92]. What a disaster! We wake with a start from this horrible nightmare and recall that these are two distinct Studies and are to be treated as unrelated, independent investigations into the same effect. What a relief!
Conclusion: Annoying Bayesian triumphalism
We all knew it would come to this, didn’t we? I’ve carefully avoided the “B” word up to this point; now it’s time to really let my anti-freq flag fly.
Error statisticians face a conundrum. Why is it necessary to account for selection effects within Studies and not across Studies? Why must we carefully avoid accounting for the possibility of contingent existence of later Studies when conducting meta-analysis? We know that this is the right thing to do — it gives the “right” answer — but no error-statistical justification for doing it this way has been offered. When we actually carry the math of contingent data collection through to its logical conclusion we find that error probabilities based on sampling distributions can’t get us there, not even post-data error probabilities like SEV.
For Bayesians this is a non-puzzle. For us this sort of distinction between intra-study and inter-study inference doesn’t exist because data enter into analyses through their likelihood function; selection effects like stopping rules and contingent investigations don’t change the likelihood and so don’t change the resulting inferences. The puzzle facing Bayesians is this: why does the severity rationale sound so darn reasonable?
When Mayo describes severity reasoning qualitatively, for example when discussing the discovery of the mechanism of prion disease, it is usually in terms of an hypothesis H and some data x that are anomalous for H. The data are treated as discrete: either an anomaly is observed or it isn’t. According to severity reasoning, to infer not-H, by (S-1) we need x to accord with it in some sense; presumably a necessary condition for this is that x should at least be possible under not-H, Pr(x; not-H) > 0. By (S-2)* the severity for inferring not-H from the anomaly x is equal to the probability that the anomaly is not observed supposing H to be the case, that is, 1 – Pr(x; H), which is monotonic decreasing in Pr(x; H). A Bayesian in this situation would quantify the evidence in favour of not-H by the likelihood ratio, Pr(x; not-H) / Pr(x; H), and provided that the numerator Pr(x; not-H) is greater than zero this is also monotonic decreasing in Pr(x; H). Since the discussion is qualitative, severity is characterized as “high” or “low” and high severity is treated as dispositive. It immediately follows that at this rather high level of abstraction likelihood ratios and severity track one another. (To a Bayesian it can appear almost as if the severity criteria were designed to agree with likelihood ratios. They weren’t, of course; it only seems so because both severity reasoning and Bayes are designed to be consistent with logic in the limit where probabilities approach 0 or 1, at least at this level of abstraction.)
So Bayesians find little to disagree with in Mayo’s accounts of severity reasoning as she describes it being applied in science, as long as the discussion remains qualitative. The more quantitative the discussion becomes the larger the divergence, reaching a maximum with optional stopping. The optional stopping setup Mayo discusses is early stopping on steroids: consider a normal model, unknown mean, known standard deviation, and a sampling design in which data collection continues just until a nominal equal-tailed 95% CI excludes zero. From Khinchin’s law of the iterated logarithm it follows that this design will eventually stop with probability 1 even when the mean is in fact zero. A Bayesian with a flat prior for the mean has equal-tailed 95% posterior credible intervals that are numerically equal to the nominal 95% CIs that set the stopping criterion, so her credible intervals exclude zero with sampling probability 1 even supposing zero is the true mean. The result is the worst possible disagreement between Bayesian inference and a severity assessment.
Many Bayesians, even the most dedicated, are troubled by consequences of stopping criteria on estimates and sampling error probabilities. Other well-known Bayesians (such as Andrew Gelman, with whom Mayo sees the possibility of an error-statistical rapprochement of sorts) are untroubled by the phenomenon. My own opinion is based on the fact that the irrelevance of stopping rules, however disquieting its consequences, goes hand-in-hand with a very desirable characteristic of Bayesian updating called the martingale property: for any measurable function on the probability space the prior expectation of the posterior expectation is equal to the prior expectation. That’s rather opaque; what it means is that we can’t predict in which direction we’ll update with certainty. Still too opaque? Okay: no ratchets, guaranteed.
In the end, I accept this disquieting property of Bayesian inference — that under at least one possible parameter value it licenses inferences that are wrong with sampling probability 1 — in return for the internal consistency of the approach and consequent virtues such as the martingale property and adherence to PRESS. On the one hand, I can never verify that the antecedent condition for certain error due to optional stopping actually holds; on the other hand, the conditions for SEV and confidence intervals to violate PRESS are purely data-dependent and thus verifiable. I can’t accept an account that can knowingly license such nonsensical inferences.
The SEV function has failed my severe test. Under severity reasoning, passing a severe test is strong warrant for a claim, but failing a severe test might still warrant a weaker claim under a less severe standard — a student that didn’t achieve an A on a test might still have gotten a B+. But I don’t affirm the severity rationale; the way I see it, Mayo’s argument for severity makes very strong claims for it, claims so strong that pathologies like failure of PRESS ought to be ruled out altogether. Having led us astray in the sequential setting, the severity argument can’t be regarded as a reliable guide at all.
What went wrong? The introduction to Proschan et al.’s chapter on inference contains the remark, “In fixed sample size trials, the test statistic, α-level, p-value, and estimated size of effect flow naturally from the same theory. Group-sequential trials cleave these relationships.” The argument for the severity rationale as applied at the most concrete level, the level where data and statistical hypotheses come into direct contact, leans heavily on the unity of frequentist statistical theory for well-behaved models with fixed sample sizes. It is precisely the complications brought on by the relevance of stopping rules to error probabilities that reveal the deficiencies of the argument. Isn’t it ironic, don’t you think?
When I first encountered the severity rationale, its prima facie plausibility was troubling to me. Was there in fact a sound philosophical basis for frequentist statistics after all? As a committed Bayesian I naturally sought to update on the possibility that it was so. The quandary I faced was that in the simple examples Mayo uses there is numerical agreement of SEV and Bayes (under reference priors); the examples couldn’t tell me whether the facial reasonability of the severity argument as applied in the examples was due to the correctness of those arguments or due to a mathematical coincidence. Now I know: this numerical agreement is a happy accident for defenders of the severity rationale, enabling them to draw on the reasonability of Bayes-licensed inferences to defend hypothesis/significance tests from criticism. I am troubled no longer.