power

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

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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)

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

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

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

But it does no such thing! [See my post from the FUSION 2016 conference here.] J. Berger, and his co-authors, will tell you the rejection ratio (and a variety of other measures created over the years) are entirely frequentist because they are created out of frequentist error statistical measures. But a creation built on frequentist measures doesn’t mean the resulting animal captures frequentist error statistical reasoning. It might be a kind of Frequentstein monster! [1]

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The Law of Comparative Support

It comes from a comparativist support position which has intrinsic plausibility, although I do not hold to it. It is akin to what some likelihoodists call “the law of support”: if H1 make the observed results probable, while H0 make them improbable, then the results are strong (or at least better) evidence for H1 compared to H0 . It appears to be saying (sensibly) that you have better evidence for a hypothesis that best “explains” the data, only this is not a good measure of explanation. It is not generally required H0 and H1 be exhaustive. Even if you hold a comparative support position, the “ratio of statistical power to significance threshold” isn’t a plausible measure for this. Now BBBS also object to the Rejection Ratio, but only largely because it’s not sensitive to the actual outcome; so they recommend the Bayes Factor post data. My criticism is much, much deeper. To get around the data-dependent part, let’s assume throughout that we’re dealing with a result just statistically significant at the α level.

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Take a one-sided Normal test T+: with n iid samples:

H0: µ ≤  0 against H1: µ >  0

σ = 10,  n = 100,  σ/√n =σx= 1,  α = .025.

So the test would reject H0 iff Z > c.025 =1.96. (1.96. is the “cut-off”.)

People often talk of a test “having a power” but the test actually specifies a power function that varies with different point values in the alternative H1 . The power of test T+ in relation to point alternative µ’ is

Pr(Z > 1.96; µ = µ’).

We can abbreviate this as POW(T+,µ’).

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Jacob Cohen’s slips

By the way, Jacob Cohen, a founder of power analysis, makes a few slips in introducing power, even though he correctly computes power through the book (so far as I know). [2] Someone recently reminded me of this, and given the confusion about power, maybe it’s had more of an ill effect than I assumed.

In the first sentence on p. 1 of Statistical Power Analysis for the Behavioral Sciences, Cohen says “The power of a statistical test is the probability it will yield statistically significant results.” Also faulty, and for two reasons, is what he says on p. 4: “The power of a statistical test of a null hypothesis is the probability that it will lead to the rejection of the null hypothesis, i.e., the probability that it will result in the conclusion that the phenomenon exists.”

Do you see the two mistakes? 

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Examples of alternatives against which T+ has high power:

  • If we add σx (i.e.,σ/√n) to the cut-off  (1.96) we are at an alternative value for µ that test T+ has .84 power to detect. In this example, σx = 1.
  • If we add 3σto the cut-off we are at an alternative value for µ that test T+ has ~ .999 power to detect. This value, which we can write as µ.999 = 4.96

Let the observed outcome just reach the cut-off to reject the null, z= 1.96.

If we were to form a “rejection ratio” or a “likelihood ratio” of μ = 4.96 compared to μ0 = 0 using

[POW(T+, 4.96)]/α,

it would be 40.  (.999/.025).

It is absurd to say the alternative 4.96 is supported 40 times as much as the null, even understanding support as comparative likelihood or something akin. The data 1.96 are even closer to 0 than to 4.96. The same point can be made with less extreme cases.) What is commonly done next is to assign priors of .5 to the two hypotheses, yielding

Pr(H0|z0) = 1/(1 + 40) = .024, so Pr(H1|z0) = .976.

Such an inference is highly unwarranted and would almost always be wrong. Back to our question:

Here’s my explanation for why some think it’s plausible to compute comparative evidence this way:

I presume it stems comes from the comparativist support position noted above. I’m guessing they’re reasoning as follows:

The probability is very high that z > 1.96 under the assumption that μ = 4.96.

The probability is low that z > 1.96 under the assumption that μ = μ0 = 0.

We’ve observed z= 1.96 (so you’ve observed z > 1.96).

Therefore, μ = 4.96 makes the observation more probable than does  μ = 0.

Therefore the outcome is (comparatively) better evidence for μ= 4.96 than for μ = 0.

But the “outcome” for a likelihood is to be the specific outcome, and the comparative appraisal of which hypothesis accords better with the data only makes sense when one keeps to this.

I can pick any far away alternative I like for purposes of getting high power, and we wouldn’t want to say that just reaching the cut-off (1.96) is good evidence for it! Power works in the reverse. That is,

If POW(T+,µ’) is high, then z= 1.96 is poor evidence that μ  > μ’.

That’s because were μ as great as μ’, with high probability we would have observed a larger z value (smaller p-value) than we did. Power may, if one wishes, be seen as a kind of distance measure, but (just like α) it is inverted.

(Note that our inferences take the form μ > μ’, μ < μ’, etc. rather than to a point value.) 

In fact:

if Pr(Z > z0;μ =μ’) = high , then Z = z0 is strong evidence that  μ < μ’!

Rather than being evidence for μ’, the statistically significant result is evidence against μ being as high as μ’.
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A post by Stephen Senn:

In my favorite guest post by Stephen Senn here, Senn strengthens a point from his 2008 book (p. 201), namely, that the following is “nonsense”:

[U]pon rejecting the null hypothesis, not only may we conclude that the treatment is effective but also that it has a clinically relevant effect. (Senn 2008, p. 201)

Now the test is designed to have high power to detect a clinically relevant effect (usually .8 or .9). I happen to have chosen an extremely high power (.999) but the claim holds for any alternative that the test has high power to detect. The clinically relevant discrepancy, as he describes it, is one “we should not like to miss”, but obtaining a statistically significant result is not evidence we’ve found a discrepancy that big. 

Supposing that it is, is essentially  to treat the test as if it were:

H0: μ < 0 vs H1: μ  > 4.96

This, he says,  is “ludicrous”as it:

would imply that we knew, before conducting the trial, that the treatment effect is either zero or at least equal to the clinically relevant difference. But where we are unsure whether a drug works or not, it would be ludicrous to maintain that it cannot have an effect which, while greater than nothing, is less than the clinically relevant difference. (Senn, 2008, p. 201)

The same holds with H0: μ = 0 as null.

If anything, it is the lower confidence limit that we would look at to see what discrepancies from 0 are warranted. The lower .975 limit (if one-sided) or .95 (if two-sided) would be 0 and .3, respectively. So we would be warranted in inferring from z:

μ  > 0 or μ  > .3.

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What does the severe tester say?

In sync with the confidence interval, she would say SEV(μ > 0) = .975 (if one-sided), and would also note some other benchmarks, e.g., SEV(μ > .96) = .84.

Equally important for her is a report of what is poorly warranted. In particular the claim that the data indicate

μ > 4.96

would be wrong over 99% of the time!

Of course, I would want to use the actual result, rather than the cut-off for rejection (as with power) but the reasoning is the same, and here I deliberately let the outcome just hit the cut-off for rejection.

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The (Type 1, 2 error probability) trade-off vanishes

Notice what happens if we consider the “real Type 1 error” as Pr(H0|z0)

Since Pr(H0|z0) decreases with increasing power, it decreases with decreasing Type 2 error. So we know that to identify “Type 1 error” and Pr(H0|z0) is to use language in a completely different way than the one in which power is defined. For there we must have a trade-off between Type 1 and 2 error probabilities.

Upshot

Using size/ power as a likelihood ratio, or even as a preregistrated estimate of expected strength of evidence (with which to accord a rejection) is problematic. The error statistician is not in the business of making inferences to point values, nor to comparative appraisals of different point hypotheses. It’s not unusual for criticisms to start out forming these ratios, and then blame the “tail areas” for exaggerating the evidence against the test hypothesis. We don’t form those ratios. But the pre-data Rejection Ratio is also misleading as an assessment alleged to be akin to a Bayes ratio or likelihood assessment. You can marry frequentist components and end up with something frequentsteinian.

REFERENCES

Bayarri, M., Benjamin, D., Berger, J., & Sellke, T. (2016, in press). “Rejection Odds and Rejection Ratios: A Proposal for Statistical Practice in Testing Hypotheses“, Journal of Mathematical Psychology

Benjamin, D. & Berger J. 2016. “Comment: A Simple Alternative to P-values,” The American Statistician (online March 7, 2016).

Cohen, J. 1988. Statistical Power Analysis for the Behavioral Sciences. 2nd ed. Hillsdale, NJ: Erlbaum.

Mayo, D. 2016. “Don’t throw out the Error Control Baby with the Error Statistical Bathwater“. (My comment on the ASA document)

Mayo, D. 2003. Comments on J. Berger’s, “Could Jeffreys, Fisher and Neyman have Agreed on Testing?  (pp. 19-24)

*Mayo, D. Statistical Inference as Severe Testing, forthcoming (2017) CUP.

Senn, S. 2008. Statistical Issues in Drug Development, 2nd ed. Chichster, New Sussex: Wiley Interscience, John Wiley & Sons.

Wasserstein, R. & Lazar, N. 2016. “The ASA’s Statement on P-values: Context, Process and Purpose”, The American Statistician (online March 7, 2016).

[1] I don’t say there’s no context where the Rejection Ratio has a frequentist role. It may arise in a diagnostic screening or empirical Bayesian context where one has to deal with a dichotomy. See, for example, this post (“Beware of questionable front page articles telling you to beware…”)

[2] It may also be found in Neyman! (Search this blog under Neyman’s Nursery.) However, Cohen uniquely provides massive power computations, before it was all computerized.

Categories: Bayesian/frequentist, fallacy of rejection, J. Berger, power, S. Senn | 8 Comments

How to tell what’s true about power if you’re practicing within the error-statistical tribe

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This is a modified reblog of an earlier post, since I keep seeing papers that confuse this.

Suppose you are reading about a result x  that is just statistically significant at level α (i.e., P-value = α) in 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. 

I have heard some people say:

A. If the test’s power to detect alternative µ’ is very low, then the just statistically significant x is poor evidence of a discrepancy (from the null) corresponding to µ’.  (i.e., there’s poor evidence that  µ > µ’ ).*See point on language in notes.

They will generally also hold that if POW(µ’) is reasonably high (at least .5), then the inference to µ > µ’ is warranted, or at least not problematic.

I have heard other people say:

B. If the test’s power to detect alternative µ’ is very low, then the just statistically significant x is good evidence of a discrepancy (from the null) corresponding to µ’ (i.e., there’s good evidence that  µ > µ’).

They will generally also hold that if POW(µ’) is reasonably high (at least .5), then the inference to µ > µ’ is unwarranted.

Which is correct, from the perspective of the (error statistical) philosophy, within which power and associated tests are defined? Continue reading

Categories: power, reforming the reformers | 17 Comments

“Nonsignificance Plus High Power Does Not Imply Support for the Null Over the Alternative.”

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Seeing the world through overly rosy glasses

Taboos about power nearly always stem from misuse of power analysis. Sander Greenland (2012) has a paper called “Nonsignificance Plus High Power Does Not Imply Support for the Null Over the Alternative.”  I’m not saying Greenland errs; the error would be made by anyone who interprets power analysis in a manner giving rise to Greenland’s objection. So what’s (ordinary) power analysis?

(I) Listen to Jacob Cohen (1988) introduce Power Analysis

“PROVING THE NULL HYPOTHESIS. Research reports in the literature are frequently flawed by conclusions that state or imply that the null hypothesis is true. For example, following the finding that the difference between two sample means is not statistically significant, instead of properly concluding from this failure to reject the null hypothesis that the data do not warrant the conclusion that the population means differ, the writer concludes, at least implicitly, that there is no difference. The latter conclusion is always strictly invalid, and is functionally invalid as well unless power is high. The high frequency of occurrence of this invalid interpretation can be laid squarely at the doorstep of the general neglect of attention to statistical power in the training of behavioral scientists. Continue reading

Categories: Cohen, Greenland, power, Statistics | 46 Comments

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

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

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

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

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

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

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

Categories: J. Berger, power, reforming the reformers, S. Senn, Statistical power, Statistics | 36 Comments

When the rejection ratio (1 – β)/α turns evidence on its head, for those practicing in an error-statistical tribe (ii)

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I’m about to hear Jim Berger give a keynote talk this afternoon at a FUSION conference I’m attending. The conference goal is to link Bayesian, frequentist and fiducial approaches: BFF.  (Program is here. See the blurb below [0]).  April 12 update below*. Berger always has novel and intriguing approaches to testing, so I was especially curious about the new measure.  It’s based on a 2016 paper by Bayarri, Benjamin, Berger, and Sellke (BBBS 2016): Rejection Odds and Rejection Ratios: A Proposal for Statistical Practice in Testing Hypotheses. They recommend:

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

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

If you’re seeking a comparative probabilist measure, the ratio of power/size can look like a likelihood ratio in favor of the alternative. To a practicing member of an error statistical tribe, however, whether along the lines of N, P, or F (Neyman, Pearson or Fisher), things can look topsy turvy. Continue reading

Categories: confidence intervals and tests, power, Statistics | 31 Comments

How to avoid making mountains out of molehills, using power/severity

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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. (As soon as it 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’).

Continue reading

Categories: fallacy of rejection, power, Statistics | 20 Comments

Telling What’s True About Power, if practicing within the error-statistical tribe

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Suppose you are reading about 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. 

I have heard some people say [0]:

A. If the test’s power to detect alternative µ’ is very low, then the statistically significant x is poor evidence of a discrepancy (from the null) corresponding to µ’.  (i.e., there’s poor evidence that  µ > µ’ ).*See point on language in notes.

They will generally also hold that if POW(µ’) is reasonably high (at least .5), then the inference to µ > µ’ is warranted, or at least not problematic.

I have heard other people say:

B. If the test’s power to detect alternative µ’ is very low, then the statistically significant x is good evidence of a discrepancy (from the null) corresponding to µ’ (i.e., there’s good evidence that  µ > µ’).

They will generally also hold that if POW(µ’) is reasonably high (at least .5), then the inference to µ > µ’ is unwarranted.

Which is correct, from the perspective of the (error statistical) philosophy, within which power and associated tests are defined?

Allow the test assumptions are adequately met. I have often said on this blog, and I repeat, the most misunderstood and abused (or unused) concept from frequentist statistics is that of a test’s power to reject the null hypothesis under the assumption alternative µ’ is true: POW(µ’). I deliberately write it in this correct manner because it is faulty to speak of the power of a test without specifying against what alternative it’s to be computed. It will also get you into trouble if you define power as in the first premise in a recent post: Continue reading

Categories: confidence intervals and tests, power, Statistics | 36 Comments

Spot the power howler: α = ß?

Spot the fallacy!

  1. METABLOG QUERYThe power of a test is the probability of correctly rejecting the null hypothesis. Write it as 1 – β.
  2. So, the probability of incorrectly rejecting the null hypothesis is β.
  3. But the probability of incorrectly rejecting the null is α (the type 1 error probability).

So α = β.

I’ve actually seen this, and variants on it [i].

[1] Although they didn’t go so far as to reach the final, shocking, deduction.

 

Categories: Error Statistics, power, Statistics | 12 Comments

No headache power (for Deirdre)

670px-Relieve-a-Tension-Headache-Step-6Bullet1

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Deirdre McCloskey’s comment leads me to try to give a “no headache” treatment of some key points about the power of a statistical test. (Trigger warning: formal stat people may dislike the informality of my exercise.)

We all know that for a given test, as the probability of a type 1 error goes down the probability of a type 2 error goes up (and power goes down).

And as the probability of a type 2 error goes down (and power goes up), the probability of a type 1 error goes up. Leaving everything else the same. There’s a trade-off between the two error probabilities.(No free lunch.) No headache powder called for.

So if someone said, as the power increases, the probability of a type 1 error decreases, they’d be saying: As the type 2 error decreases, the probability of a type 1 error decreases! That’s the opposite of a trade-off. So you’d know automatically they’d made a mistake or were defining things in a way that differs from standard NP statistical tests.

Before turning to my little exercise, I note that power is defined in terms of a test’s cut-off for rejecting the null, whereas a severity assessment always considers the actual value observed (attained power). Here I’m just trying to clarify regular old power, as defined in a N-P test.

^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^

Let’s use a familiar oversimple example to fix the trade-off in our minds so that it cannot be dislodged. Our old friend, test T+ : We’re testing the mean of a Normal distribution with n iid samples, and (for simplicity) known, fixed σ:

H0: µ ≤  0 against H1: µ >  0

Let σ = 2n = 25, so (σ/ √n) = .4. To avoid those annoying X-bars, I will use M for the sample mean. I will abbreviate (σ/ √n) as σx .

  • Test T+ is a rule: reject Hiff M > m*
  • Power of a test T+ is computed in relation to values of µ >  0.
  • The power of T+ against alternative µ =µ= Pr(T+ rejects H0 ;µ = µ1) = Pr(M > m*; µ = µ1)

We may abbreviate this as : POW(T+,α, µ = µ1) Continue reading

Categories: power, statistical tests, Statistics | 6 Comments

To raise the power of a test is to lower (not raise) the “hurdle” for rejecting the null (Ziliac and McCloskey 3 years on)

Part 2 Prionvac: The Will to Understand PowerI said I’d reblog one of the 3-year “memory lane” posts marked in red, with a few new comments (in burgundy), from time to time. So let me comment on one referring to Ziliac and McCloskey on power. (from Oct.2011). I would think they’d want to correct some wrong statements, or explain their shifts in meaning. My hope is that, 3 years on, they’ll be ready to do so. By mixing some correct definitions with erroneous ones, they introduce more confusion into the discussion.

From my post 3 years ago: “The Will to Understand Power”: In this post, I will adhere precisely to the text, and offer no new interpretation of tests. Type 1 and 2 errors and power are just formal notions with formal definitions.  But we need to get them right (especially if we are giving expert advice).  You can hate the concepts; just define them correctly please.  They write:

“The error of the second kind is the error of accepting the null hypothesis of (say) zero effect when the null is in face false, that is, then (say) such and such a positive effect is true.”

So far so good (keeping in mind that “positive effect” refers to a parameter discrepancy, say δ, not an observed difference.

And the power of a test to detect that such and such a positive effect δ is true is equal to the probability of rejecting the null hypothesis of (say) zero effect when the null is in fact false, and a positive effect as large as δ is present.

Fine.

Let this alternative be abbreviated H’(δ):

H’(δ): there is a positive effect as large as δ.

Suppose the test rejects the null when it reaches a significance level of .01.

(1) The power of the test to detect H’(δ) =

P(test rejects null at .01 level; H’(δ) is true).

Say it is 0.85.

“If the power of a test is high, say, 0.85 or higher, then the scientist can be reasonably confident that at minimum the null hypothesis (of, again, zero effect if that is the null chosen) is false and that therefore his rejection of it is highly probably correct”. (Z & M, 132-3).

But this is not so.  Perhaps they are slipping into the cardinal error of mistaking (1) as a posterior probability:

(1’) P(H’(δ) is true| test rejects null at .01 level)! Continue reading

Categories: 3-year memory lane, power, Statistics | Tags: , , | 6 Comments

Neyman, Power, and Severity

April 16, 1894 – August 5, 1981

NEYMAN: April 16, 1894 – August 5, 1981

Jerzy Neyman: April 16, 1894-August 5, 1981. This reblogs posts under “The Will to Understand Power” & “Neyman’s Nursery” here & here.

Way back when, although I’d never met him, I sent my doctoral dissertation, Philosophy of Statistics, to one person only: Professor Ronald Giere. (And he would read it, too!) I knew from his publications that he was a leading defender of frequentist statistical methods in philosophy of science, and that he’d worked for at time with Birnbaum in NYC.

Some ten 15 years ago, Giere decided to quit philosophy of statistics (while remaining in philosophy of science): I think it had to do with a certain form of statistical exile (in philosophy). He asked me if I wanted his papers—a mass of work on statistics and statistical foundations gathered over many years. Could I make a home for them? I said yes. Then came his caveat: there would be a lot of them.

As it happened, we were building a new house at the time, Thebes, and I designed a special room on the top floor that could house a dozen or so file cabinets. (I painted it pale rose, with white lacquered book shelves up to the ceiling.) Then, for more than 9 months (same as my son!), I waited . . . Several boxes finally arrived, containing hundreds of files—each meticulously labeled with titles and dates.  More than that, the labels were hand-typed!  I thought, If Ron knew what a slob I was, he likely would not have entrusted me with these treasures. (Perhaps he knew of no one else who would  actually want them!) Continue reading

Categories: Neyman, phil/history of stat, power, Statistics | Tags: , , , | 5 Comments

A. Spanos: “Recurring controversies about P values and confidence intervals revisited”

A SPANOS

Aris Spanos
Wilson E. Schmidt Professor of Economics
Department of Economics, Virginia Tech

Recurring controversies about P values and confidence intervals revisited*
Ecological Society of America (ESA) ECOLOGY
Forum—P Values and Model Selection (pp. 609-654)
Volume 95, Issue 3 (March 2014): pp. 645-651

INTRODUCTION

The use, abuse, interpretations and reinterpretations of the notion of a P value has been a hot topic of controversy since the 1950s in statistics and several applied fields, including psychology, sociology, ecology, medicine, and economics.

The initial controversy between Fisher’s significance testing and the Neyman and Pearson (N-P; 1933) hypothesis testing concerned the extent to which the pre-data Type  I  error  probability  α can  address the arbitrariness and potential abuse of Fisher’s post-data  threshold for the value. Continue reading

Categories: CIs and tests, Error Statistics, Fisher, P-values, power, Statistics | 32 Comments

Power taboos: Statue of Liberty, Senn, Neyman, Carnap, Severity

Unknown-3Is it taboo to use a test’s power to assess what may be learned from the data in front of us? (Is it limited to pre-data planning?) If not entirely taboo, some regard power as irrelevant post-data[i], and the reason I’ve heard is along the lines of an analogy Stephen Senn gave today (in a comment discussing his last post here)[ii].

Senn comment: So let me give you another analogy to your (very interesting) fire alarm analogy (My analogy is imperfect but so is the fire alarm.) If you want to cross the Atlantic from Glasgow you should do some serious calculations to decide what boat you need. However, if several days later you arrive at the Statue of Liberty the fact that you see it is more important than the size of the boat for deciding that you did, indeed, cross the Atlantic.

My fire alarm analogy is here. My analogy presumes you are assessing the situation (about the fire) long distance. Continue reading

Categories: exchange with commentators, Neyman's Nursery, P-values, Phil6334, power, Stephen Senn | 6 Comments

Stephen Senn: “Delta Force: To what extent is clinical relevance relevant?” (Guest Post)

Stephen Senn

Senn

Stephen Senn
Head, Methodology and Statistics Group,
Competence Center for Methodology and Statistics (CCMS),
Luxembourg

Delta Force
To what extent is clinical relevance relevant?

Inspiration
This note has been inspired by a Twitter exchange with respected scientist and famous blogger  David Colquhoun. He queried whether a treatment that had 2/3 of an effect that would be described as clinically relevant could be useful. I was surprised at the question, since I would regard it as being pretty obvious that it could but, on reflection, I realise that things that may seem obvious to some who have worked in drug development may not be obvious to others, and if they are not obvious to others are either in need of a defence or wrong. I don’t think I am wrong and this note is to explain my thinking on the subject. Continue reading

Categories: power, Statistics, Stephen Senn | 39 Comments

Get empowered to detect power howlers

questionmark pinkIf a test’s power to detect µ’ is low then a statistically significant result is good/lousy evidence of discrepancy µ’? Which is it?

If your smoke alarm has little capability of triggering unless your house is fully ablaze, then if it has triggered, is that a strong or weak indication of a fire? Compare this insensitive smoke alarm to one that is so sensitive that burning toast sets it off. The answer is: that the alarm from the insensitive detector is triggered is a good indication of the presence of (some) fire, while hearing the ultra sensitive alarm go off is not.[i]

Yet I often hear people say things to the effect that: Continue reading

Categories: confidence intervals and tests, power, Statistics | 34 Comments

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