Question: Why do we settle for 80% power? Answer: We’re confused.

Coming back to the topic of my previous post, about how we must draw distinct conclusions from different hypothesis test procedures, I’d like to show an example of how these confusions might actually arise in practice. The following example comes from Royall’s book (you really should read it), and questions why we settle for a power of only 80%. It’s a question we’ve probably all thought about at some point. Isn’t 80% power just as arbitrary as p-value thresholds? And why should we settle for such a large probability of error before we even start an experiment?

From Royall (1997, pp. 109-110):

Why is a power of only 0.80 OK?

We begin with a mild peculiarity — why is it that the Type I error rate α is ordinarily required to be 0.05 or 0.01, but a Type II error rate as large as 0.20 is regularly adopted? This often occurs when the sample size for a clinical trial is being determined. In trials that compare a new treatment to an old one, the ‘null’ hypothesis usually states that the new treatment is not better than the old, while the alternative states that it is. The specific alternative value chosen might be suggested by pilot studies or uncontrolled trials that preceded the experiment that is now being planned, and the sample size is determined [by calculating power] with α = 0.05 and β = 0.20. Why is such a large value of β acceptable? Why the severe asymmetry in favor of α? Sometimes, of course, a Type I error would be much more costly than a Type II error would be (e.g. if the new treatment is much more expensive, or if it entails greater discomfort). But sometimes the opposite is true, and we never see studies proposed with α = 0.20 and β = 0.05. No one is satisfied to report that ‘the new treatment is statistically significantly better than the old (p ≤ 0.20)’.

Often the sample-size calculation is first made with β = α = 0.05. But in that case experimenters are usually quite disappointed to see what large values of n are required, especially in trials with binomial (success/failure) outcomes. They next set their sights a bit lower, with α = 0.05 and β = 0.10, and find that n is still ‘too large’. Finally they settle for α = 0.05 and β = 0.20.

Why do they not adjust α and settle for α = 0.20 and β = 0.05? Why is small α a non-negotiable demand, while small β is only a flexible desideratum? A large α would seem to be scientifically unacceptable, indicating a lack of rigor, while a large β is merely undesirable, an unfortunate but sometimes unavoidable consequence of the fact that observations are expensive or that subjects eligible for the trial are hard to find and recruit. We might have to live with a large β, but good science seems to demand that α be small.

What is happening is that the formal Neyman-Pearson machinery is being used, but it is being given a rejection-trial interpretation (Emphasis added). The quantities α and β are not just the respective probabilities of choosing one hypothesis when the other is true; if they were, then calling the first hypothesis H2 and the second H1 would reverse the roles of α and β, and α = 0.20, β = 0.05 would be just as satisfactory for the problem in its new formulation as α = 0.05 and β = 0.20 were in the old one. The asymmetry arises because the quantity α is being used in the dual roles that it plays in rejection trials — it is both the probability of rejecting a hypothesis when that hypothesis is true and the measure of strength of the evidence needed to justify rejection. Good science demands small α because small α is supposed to mean strong evidence. On the other hand, the Type II error probability β is being interpreted simply as the probability of failing to find strong evidence against H1 when the alternative H2 is true (Emphasis added. Recall Fisher’s quote about the impossibility of making Type II errors since we never accept the null.) … When observations are expensive or difficult to obtain we might indeed have to live with a large probability of failure to find strong evidence. In fact, when the expense or difficulty is extreme, we often decide not to do the experiment at all, thereby accpeting values of α = 0 and β = [1].

— End excerpt.

So there we have our confusion, which I alluded to in the previous post. We are imposing rejection-trial reasoning onto the Neyman-Pearson decision framework. We accept a huge β because we interpret our results as a mere failure (to produce strong enough evidence) to reject the null, when really our results imply a decision to accept the ‘null’. Remember, with NP we are always forced to choose between two hypotheses — we can never abstain from this choice because the respective rejection regions for H1 and H2 encompass the entire sample space by definition; that is, any result obtained must fall into one of the rejection regions we’ve defined. We can adjust either α or β (before starting the experiment) as we see fit, based on the relative costs of these errors. Since neither hypothesis is inherently special, adjusting α is as justified as adjusting β and neither has any bearing on the strength of evidence from our experiment.

And surely it doesn’t matter which hypothesis is defined as the null, because then we would just switch the respective α and β — that is, H1 and H2 can be reversed without any penalty in the NP framework. Who cares which hypothesis gets the label 1 or 2?

But imagine the outrage (and snarky blog posts) if we tried swapping out the null hypothesis with our pet hypothesis in a rejection trial. Would anybody buy it if we tried to accept our pet hypothesis simply based on a failure to reject it? Of course not, because that would be absurd. Failing to find strong evidence against a single hypothesis has no logical implication that we have found evidence for that hypothesis. Fisher was right about this one. And this is yet another reason NP procedures and rejection trials don’t mix.

However, when we are using concepts of power and Type II errors, we are working with NP procedures which are completely symmetrical and have no concept of strength of evidence per se. Failure to reject the null hypothesis has the exact same meaning as accepting the null hypothesis — they are simply different ways to say the same thing.  If what you want is to measure evidence, fine; I think we should be measuring evidence in any case. But then you don’t have a relevant concept of power, as Fisher has reiterated time and time again. If you want to use power to help plan experiments (as seems to be recommended just about everywhere you look) then you must cast aside your intuitions about interpreting observations from that experiment as evidence. You must reject the rejection trial and reject notions of statistical evidence. 

Or don’t, but then you’re swimming in a sea of confusion.

 

References

Royall, R. (1997). Statistical evidence: a likelihood paradigm (Vol. 71). CRC press.

Are all significance tests made of the same stuff?

No! If you are like most of the sane researchers out there, you don’t spend your days and nights worrying about the nuances of different statistical concepts. Especially ones as traditional as these. But there is one concept that I think we should all be aware of: P-values mean very different things to different people. Richard Royall (1997, p. 76-7) provides a smattering of different possible interpretations and fleshes out the arguments for why these mixed interpretations are problematic (much of this post comes from his book):

In the testing process the null hypothesis either is rejected or is not rejected. If the null hypothesis is not rejected, we will say that the data on which the test is based do not provide sufficient evidence to cause rejection. (Daniel, 1991, p. 192)

A nonsignificant result does not prove that the null hypothesis is correct — merely that it is tenable — our data do not give adequate grounds for rejecting it. (Snedecor and Cochran, 1980, p. 66)

The verdict does not depend on how much more readily some other hypothesis would explain the data. We do not even start to take that question seriously until we have rejected the null hypothesis. …..The statistical significance level is a statement about evidence… If it is small enough, say p = 0.001, we infer that the result is not readily explained as a chance outcome if the null hypothesis is true and we start to look for an alternative explanation with considerable assurance. (Murphy, 1985, p. 120)

If [the p-value] is small, we have two explanations — a rare event has happened, or the assumed distribution is wrong. This is the essence of the significance test argument. Not to reject the null hypothesis … means only that it is accepted for the moment on a provisional basis. (Watson, 1983)

Test of hypothesis. A procedure whereby the truth or falseness of the tested hypothesis is investigated by examining a value of the test statistic computed from a sample and then deciding to reject or accept the tested hypothesis according to whether the value falls into the critical region or acceptance region, respectively. (Remington and Schork, 1970, p. 200)

Although a ‘significant’ departure provides some degree of evidence against a null hypothesis, it is important to realize that a ‘nonsignificant’ departure does not provide positive evidence in favour of that hypothesis. The situation is rather that we have failed to find strong evidence against the null hypothesis. (Armitage and Berry, 1987, p. 96)

If that value [of the test statistic] is in the region of rejection, the decision is to reject H0; if that value is outside the region of rejection, the decision is that H0 cannot be rejected at the chosen level of significance … The reasoning behind this decision process is very simple. If the probability associated with the occurance under the null hypothesis of a particular value in the sampling distribution is very small, we may explain the actual occurrence of that value in two ways; first we may explain it by deciding that the null hypothesis is false or, second, we may explain it by deciding that a rare and unlikely event has occurred. (Siegel and Castellan, 1988, Chapter 2)

These all mix and match three distinct viewpoints with regard to hypothesis tests: 1) Neyman-Pearson decision procedures, 2) Fisher’s p-value significance tests, and 3) Fisher’s rejection trials (I think 2 and 3 are sufficiently different to be considered separately). Mixing and matching them is inappropriate, as will be shown below. Unfortunately, they all use the same terms so this can get confusing! I’ll do my best to keep things simple.

1. Neyman-Pearson (NP) decision procedure:
Neyman describes it thusly:

The problem of testing a statistical hypothesis occurs when circumstances force us to make a choice between two courses of action: either take step A or take step B… (Neyman 1950, p. 258)

…any rule R prescribing that we take action A when the sample point … falls within a specified category of points, and that we take action B in all other cases, is a test of a statistical hypothesis. (Neyman 1950, p. 258)

The terms ‘accepting’ and ‘rejecting’ a statistical hypothesis are very convenient and well established. It is important, however, to keep their exact meaning in mind and to discard various additional implications which may be suggested by intuition. Thus, to accept a hypothesis H means only to take action A rather than action B. This does not mean that we necessarily believe that the hypothesis H is true. Also if the application … ‘rejects’ H, this means only that the rule prescribes action B and does not imply that we believe that H is false. (Neyman 1950, p. 259)

So what do we take from this? NP testing is about making a decision to choose H0 or H1, not about shedding light on the truth of any one hypothesis or another. We calculate a test statistic, see where it lies with regard to our predefined rejection regions, and make the corresponding decision. We can assure that we are not often wrong by defining Type I and Type II error probabilities (α and β) to be used in our decision procedure. According to this framework, a good test is one that minimizes these long-run error probabilities. It is important to note that this procedure cannot tell us anything about the truth of hypotheses and does not provide us with a measure of evidence of any kind, only a decision to be made according to our criteria. This procedure is notably symmetric — that is, we can either choose H0 or H1.

Test results would look like this:

α and β were prespecified -based on relevant costs associated with the different errors- for this situation at yadda yadda yadda. The test statistic (say, t=2.5) falls inside the rejection region for H0 defined as t>2.0 so we reject H0 and accept H1.” (Alternatively, you might see “p < α = x so we reject H0. The exact value of p is irrelevant, it is either inside or outside of the rejection region defined by α. Obtaining a p = .04 is effectively equivalent to p = .001 for this procedure, as is obtaining a result very much larger than the critical t above.)

2. Fisher’s p-value significance tests 

Fisher’s first procedure is only ever concerned with one hypothesis- that being the null. This procedure is not concerned with making decisions (and when in science do we actually ever do that anyway?) but with measuring evidence against the hypothesis. We want to evaluate ‘the strength of evidence against the hypothesis’ (Fisher, 1958, p.80) by evaluating how rare our particular result (or even bigger results) would be if there were really no effect in the study. Our objective here is to calculate a single number that Fisher called the level of significance, or the p-value. Smaller p is more evidence against the hypothesis than larger p. Increasing levels of significance* are often represented** by more asterisks*** in tables or graphs. More asterisks mean lower p-values, and presumably more evidence against the null.

What is the rationale behind this test? There are only two possible interpretations of our low p: either a rare event has occurred, or the underlying hypothesis is false. Fisher doesn’t think the former is reasonable, so we should assume the latter (Bakan, 1966).

Note that this procedure is directly trying to measure the truth value of a hypothesis. Lower ps indicate more evidence against the hypothesis. This is based on the Law of Improbability, that is,

Law of Improbability: If hypothesis A implies that the probability that a random variable X takes on the value x is quite small, say p(x), then the observation X = x is evidence against A, and the smaller p(x), the stronger the evidence. (Royall, 1997, p. 65)

In a future post I will attempt to show why this law is not a valid indicator of evidence. For the purpose of this post we just need to understand the logic behind this test and that it is fundamentally different from NP procedures. This test alone does not provide any guidance with regard to taking action or making a decision, it is intended as a measure of evidence against a hypothesis.

Test results would look like this:

The present results obtain a t value of 2.5, which corresponds to an observed p = .01**. This level of significance is very small and indicates quite strong evidence against the hypothesis of no difference.

3. Fisher’s rejection trials

This is a strange twist on both of the other procedures above, taking elements from each to form a rejection trial. This test is a decision procedure, much like NP procedures, but with only one explicitly defined hypothesis, a la p-value significance tests. The test is most like what psychologists actually use today, framed as two possible decisions, again like NP, but now they are framed in terms of only one hypothesis. Rejection regions are back too, defined as a region of values that have small probability under H0 (i.e., defined by a small α). It is framed as a problem of logic, specifically,

…a process analogous to testing a proposition in formal logic via the argument known as modus tollens, or ‘denying the consequent’: if A implies B, then not-B implies not-A. We can test A by determining whether B is true. If B is false, then we conclude that A is false. But, on the other hand, if B is found to be true we cannot conclude that A is true. That is, A can be proven false by such a test but it cannot be proven true — either we disprove A or we fail to disprove it…. When B is found to be true, so that A survives the test, this result, although not proving A, does seem intuitively to be evidence supporting A. (Royall, 1997, p. 72)

An important caveat is that these tests are probabilistic in nature, so the logical implications aren’t quite right. Nevertheless, rejection trials are what Fisher referred to when he famously said,

Every experiment may be said to exist only in order to give the facts a chance of disproving the null hypothesis… The notion of an error of the so-called ‘second kind,’ due to accepting the null hypothesis ‘when it is false’ … has no meaning with reference to simple tests of significance. (Fisher, 1966)

So there is a major difference from NP — With rejection trials you have a single hypothesis (as opposed to 2) combined with decision rules of “reject the H0 or do not reject H0” (as opposed to reject H0/H1 or accept H0/H1). With rejection trials we are back to making a decision. This test is asymmetric (as opposed to NP which is symmetric) — that is, we can only ever reject H0, never accept it.

While we are making decisions with rejection trials, the decisions have a different meaning than that of NP procedures. In this framework, deciding to reject H0 implies the hypothesis is “inconsistent with the data” or that the data “provide sufficient evidence to cause rejection” of the hypothesis (Royall, 1997, p.74). So rejection trials are intended to be both decision procedures and measures of evidence. Test statistics that fall into smaller α regions are considered stronger evidence, much the same way that a smaller p-value indicates more evidence against the hypothesis. For NP procedures α is simply a property of the test, and choosing a lower one has no evidential meaning per se (although see Mayo, 1996 for a 4th significance procedure — severity testing).

Test results would look like this:

The present results obtain a t = 2.5, p = .01, which is sufficiently strong evidence against H0 to warrant its rejection.

What is the takeaway?

If you aren’t aware of the difference between the three types of hypothesis testing procedures, you’ll find yourself jumbling them all up (Gigerenzer, 2004). If you aren’t careful, you may end up thinking you have a measure of evidence when you actually have a guide to action.

Which one is correct?

Funny enough, I don’t endorse any of them. I contend that p-values never measure evidence (in either p-value procedures or rejection trials) and NP procedures lead to absurdities that I can’t in good faith accept while simultaneously endorsing them.

Why write 2000 words clarifying the nuanced differences between three procedures I think are patently worthless? Well, did you see what I said at the top referring to sane researchers?

A future post is coming that will explicate the criticisms of each procedure, many of the points again coming from Royall’s book.

References

Armitage, P., & Berry, G. (1987). Statistical methods in medical research. Oxford: Blackwell Scientific.

Bakan, D. (1966). The test of significance in psychological research.Psychological bulletin, 66(6), 423.

Daniel, W. W. (1991). Hypothesis testing. Biostatistics: a foundation for analysis in the health sciences5, 191.

Fisher, R. A. (1958).Statistical methods for research workers (13th ed.). New York: Hafner.

Fisher, R. A. (1966). The design of experiments (8th edn.) Oliver and Boyd.

Gigerenzer, G. (2004). Mindless statistics. The Journal of Socio-Economics,33(5), 587-606.

Mayo, D. G. (1996). Error and the growth of experimental knowledge. University of Chicago Press.

Murphy, E. A. (1985). A companion to medical statistics. Johns Hopkins University Press.

Neyman, J. (1950). First course in probability and statistic. Published by Henry Holt, 1950.,1.

Remington, R. D., & Schork, M. A. (1970). Statistics with applications to the biological and health sciences.

Royall, R. (1997). Statistical evidence: a likelihood paradigm (Vol. 71). CRC press.

Siegel, S. C., & Castellan, J. NJ (1988). Nonparametric statistics for the behavioural sciences. New York, McGraw-Hill.

Snedecor, G. W. WG Cochran. 1980. Statistical Methods. Iowa State Univ. Press, Ames.

Watson, G. S. (1983). Hypothesis testing. Encyclopedia of Statistics in Quality and Reliability.

The Special One-Way ANOVA (or, Shutting up Reviewer #2)

The One-Way Analysis of Variance (ANOVA) is a handy procedure that is commonly used when a researcher has three or more groups that they want to compare. If the test comes up significant, follow-up tests are run to determine which groups show meaningful differences. These follow-up tests are often corrected for multiple comparisons (the Bonferroni method is most common in my experience), dividing the nominal alpha (usually .05) by the number of tests. So if there are 5 follow up tests, each comparison’s p-value must be below .01 to really “count” as significant. This reduces the test’s power considerably, but better guards against false-positives. It is common to correct all follow-up tests after a significant main effect, no matter the experimental design, but this is unnecessary when there are only three levels. H/T to Mike Aitken Deakin (here: @mrfaitkendeakin) and  Chris Chambers (here: @chrisdc77) for sharing.

The Logic of the Uncorrected Test

In the case of the One-Way ANOVA with three levels, it is not necessary to correct for the extra t-tests because the experimental design ensures that the family-wise error rate will necessarily stay at 5% — so long as no follow-up tests are carried out when the overall ANOVA is not significant.

A family-wise error rate (FWER) is the allowed tolerance for making at least 1 erroneous rejection of the null-hypothesis in a set of tests. If we make 2, 3, or even 4 erroneous rejections, it isn’t considered any worse than 1. Whether or not this makes sense is for another blog post. But taking this definition, we can think through the scenarios (outlined in Chris’s tweet) and see why no corrections are needed:

True relationship: µ1 = µ2 = µ3 (null-hypothesis is really true, all groups equal). If the main effect is not significant, no follow-up tests are run and the FWER remains at 5%. (If you run follow-up tests at this point you do need to correct for multiple comparisons.) If the main effect is significant, it does not matter what the follow-up tests show because we have already committed our allotted false-positive. In other words, we’ve already made the higher order mistake of saying that some differences are present before we even examine the individual group contrasts. Again, the FWER accounts for making at least 1 erroneous rejection. So no matter what our follow-up tests show, the FWER remains at 5% since we have already made our first false-positive before even conducting the follow-ups.

True relationship: µ1 ≠ µ2 = µ3, OR µ1 = µ2 ≠ µ3, OR µ1 ≠ µ3 = µ2  (null-hypothesis is really false, one group stands out). If the main effect is significant then we are correct, and no false-positive is possible at this level. We go with our follow-up tests (where it is really true that one group is different from the other two), where only one pair of means is truly equal. So that single pair is the only place for a possible false-positive result. Again, our FWER remains at 5% because we only have 1 opportunity to erroneously reject a null-hypothesis.

True relationship: µ1 ≠ µ2 ≠ µ3. A false-positive is impossible in this case because all three groups are truly different. All follow-up tests necessarily keep the FWER at 0%!

There is no possible scenario where your FWER goes above 5%, so no need to correct for multiple comparisons! 

So the next time Reviewer #2 gives you a hard time about correcting for multiple comparisons on a One-Way ANOVA with three levels, you can rightfully defend your uncorrected t-tests. Not correcting the alpha saves you some power, thereby making it easier to support your interesting findings.

If you wanted to sidestep the multiple comparison problem altogether you could do a fully Bayesian analysis, in which the number of tests conducted holds no weight on the evidence of a single test. So in other words, you could jump straight to the comparisons of interest instead of doing the significant main effect → follow-up test routine. Wouldn’t that save us all a lot of hassle?

 

Lack of Power (and not the statistical kind)

One thing that never really comes up when people talk about “Questionable Research Practices,” is what to do when you’re a junior in the field and someone your senior suggests that you partake. [snip] It can be daunting to be the only one on who thinks we shouldn’t drop 2 outliers to get our p-value from .08 to .01, or who thinks we shouldn’t go collect 5 more subjects to make it “work.” When it is 1 vs 4 and you’re at the bottom of the totem pole, it rarely works out the way you want. It is hard not to get defensive, and you desperately want everyone to just come around to your thinking- but it doesn’t happen. What can the little guy say to the behemoths staring him down?

I’ve recently been put in this situation, and I am finding it to be a challenge that I don’t know how to overcome. It is difficult to explain to someone that what they are suggesting you do is [questionable] (At least not without sounding accusatory). I can explain the problems with letting our post hoc p-value guide interpretation, or the problems for replicability when the analysis plan isn’t predetermined, or the problems with cherry picking outliers, but it’s really an ethical issue at its core. I don’t want to engage in what I know is a [questionable] practice, but I don’t have a choice. I can’t afford to burn bridges when those same bridges are the only things that get me over the water and into a job.

I’ve realized that this amazing movement in the field of psychology has left me feeling somewhat helpless. When push comes to shove, the one running the lab wins and I have to yield- even against my better judgment. After six five months of data collection, am I supposed to just step away and not put my name on the work? There’s something to that, I suppose. A bit of poetic justice. But justice doesn’t get you into grad school, or get you a PhD, or get you a faculty job, or get you a grant, or get you tenure. The pressure is real for the ones at the bottom. I think more attention needs to be paid to this aspect of the psychology movement. I can’t be the only one who feels like I know what I should (and shouldn’t) be doing but don’t have a choice.

Edit: See another great point of view on this issue here http://jonathanramsay.com/questionable-research-practices-the-grad-student-perspective/

edit3: Changed some language

An undergraduate’s experience with replications

A lot of psychologists are in a bit of a tiff right now. I think everyone agrees that replications are important, but it doesn’t seem like there is a consensus for how it should go about (For many perspectives, see: here, here, here, here, here, here, here). Since Sanjay asked for more perspectives from people who aren’t tenured, I figured I’d write up my experience with replication. Take note, I graduated but I am not in graduate school yet, so I am one vulnerable puppy. Luckily my experience was very civil.

During my junior/senior year fellowship, I ran 2 identical direct replications of a psychophysics experiment and both were disappointing. I wasn’t the first person in the lab to try to replicate it either: the addition of my “failures” made it 5 collective unsuccessful replications. At what point do you throw in the towel and say, “We’re never gonna get it”? I went on to manipulate the stimuli and task and ended up finding some cool results, but the taste of sour data was still in my mouth. The worst part was that I had to slap my “failures to replicate” on a poster and travel cross-country to present them at a conference. I was nervous before presenting, because how are you supposed to explain failures to replicate in psychophysics? It’s not like social psych, where one can point to the specter of “unknown moderators” (no offense, that’s my field now).

So, how did the conference go? Very well I should think. I was not surprised by some reactions I got from viewers when I said those dreaded words, “failed to replicate,” on the order of: “Oh wow, that sucks for them,” “Welp, that’s never good,” “Oh no! He’s in my department…..that’s embarrassing,” “Did you really try 5 times? I would have stopped after 1.” The most stress-inducing part of the whole thing was when the person I was failing to replicate came up and introduced himself. I was expecting hurt feelings, or animosity. What I got was a reasonable reply from a senior in my field. He said, “Well, that’s really too bad. You never got it in 5 tries? Hmmm…. I guess we might have overestimated how robust that effect is. It could be that it is just a weak effect. We’ve moved on since then to show the effect with other stimuli but we haven’t done this exact setup again, maybe we should. Thanks for sharing with me, if you write up the manuscript I’d love it if you sent it to me when it’s done.”

What a reasonable guy. I was expecting barred teeth and a death stare, but what I got was a senior in the field who was open to revising his beliefs.

One thing to note: his comment, “if you write up the manuscript I’d love it if you sent it to me when it’s done (emphasis added)” really highlights the view that replications are likely to be dropped if they “fail.” Hopefully this special issue can change the culture and change that if to when. Thanks to Daniel Lakens (@lakens) and Brian Nosek (@BrianNosek) for trailblazing.