The Abuse of Power: The Pervasive Fallacy of Power
Calculations for Data Analysis
John M. HOENIG and Dennis M. HEISEY

It is well known that statistical power calculations can bevaluable in planning an experiment. There is also a large literature advocating that power calculations be made whenever one performs a statistical test of a hypothesis and one
obtains a statistically nonsignificant result. Advocates ofsuch post-experiment power calculations claim the calculations should be used to aid in the interpretation of theexperimental results. This approach, which appears in various forms, is fundamentally flawed. We document that the
problem is extensive and present arguments to demonstrate
the flaw in the logic.
KEY WORDS: Bioequivalence testing; Burden of proof;
Observed power; Retrospective power analysis; Statisticalpower; Type II error.

1.

INTRODUCTION

It is well known among applied scientists that a lack ofimpact or effect is not sufficiently established by a failure
to demonstrate statistical significance. A failure to reject
the null hypothesis of no effect may be the result of low
statistical power when an important effect actually exists
and the null hypothesis of no effect is in fact false. This canbe called the dilemma of the nonrejected null hypothesis:
what should we do when we fail to reject a hypothesis?
Dismayingly, there is a large, current literature that advocates the inappropriate use of post-experiment power calculations as a guide to interpreting tests with statisticallynonsignificant results. These ideas are held tenaciously in avariety of disciplines as evidenced by methodological recommendations in 19 applied journals (Table 1). In our experience as consulting statisticians, authors are not infrequently required to perform such calculations by journal
reviewers or editors; at least two journals ask for these calculations as a matter of policy (Anon. 1995; Anon. 1998).
We emphasize that these calculations are sought primarily
with the thought that they are useful for explaining the observed data, rather than for the purpose of planning somefuture experiment. We even found statistical textbooks thatJohn M. Hoenig is Professor, Virginia Institute of Marine Science, College of William and Mary, Gloucester Point, VA 23062 (E-mail: hoenig@
vims.edu). Dennis M. Heisey is Statistician, Department of Surgery andDepartment of Biostatistics and Medical Informatics, University of Wisconsin, Madison, WI 53792. Order of authorship determined by randomization. The authors thank Marilyn Lewis for research assistance and theanonymous reviewers for helpful comments. This is VIMS Contribution
No. 2335.

c 2001 American Statistical Association

illustrate the flawed approach (e.g., Rosner 1990; Winer,
Brown, and Michels 1991; Zar 1996). Researchers need tobe made aware of the shortcomings of power calculations
as data analytic tools and taught more appropriate methodology.
It is important to understand the motivation of appliedscientists for using power analysis to interpret hypothesis
tests with nonsignificant results. The traditional, widely accepted standard has been to protect the investigator fromfalsely concluding that some treatment has an effect when
indeed it has none. However, there is increasing recognition
that a “reversal of the usual scientific burden of proof” (e.g.,
Dayton 1998) is preferred in many areas of scientific inference. Areas where this is a particular concern include making decisions about environmental impacts, product safety,
and public welfare where some people want to be protectedfrom failing to reject a null hypothesis of no impact whena serious (e.g., harmful or dangerous) effect exists. We believe that the post-hoc power approaches that have consequently arisen are due to applied scientists being heavily
tradition-bound to test the usual “no impact null hypothesis,” despite it not always being the relevant null hypothesis
for the question at hand.
We describe the flaws in trying to use power calculations
for data-analytic purposes and suggest that statistics courses
should have more emphasis on the investigator’s choice of
hypotheses and on the interpretation of confidence intervals.
We also suggest that introducing the concept of equivalence
testing may help students understand hypothesis tests. For
pedagogical reasons, we have kept our explanations as simple as possible.
2.

INAPPROPRIATE USES OF POWER ANALYSIS

2.1 “Observed Power”
There are two common applications of power analysis
when a nonrejected null hypothesis occurs. The first is
to compute the power of the test for the observed valueof the test statistic. That is, assuming the observed treatment effects and variability are equal to the true parameter values, the probability of rejecting the null hypothesis
is computed. This is sometimes referred to as “observed
power.” Several widely distributed statistical software packages, such as SPSS, provide observed power in conjunction
with data analyses (see Thomas and Krebs 1997). Advocates of observed power argue that there is evidence forthe null hypothesis being true if statistical significance was
not achieved despite the computed power being high at theobserved effect size. (Usually, this is stated in terms of theevidence for the null hypothesis (no effect) being weak if
observed power was low.)
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Table 1. Journals with Articles Advocating Post-Experiment Power
Analysis
American Journal of Physical Anthropology: Hodges and Schell (1988)
American Naturalist: Toft and Shea (1983); Rotenberry and Wiens (1985)*Animal Behavior: Thomas and Juanes (1996); Anon. (1998)
Aquaculture: Searcy-Bernal (1994)
Australian Journal of Marine and Freshwater Research:
Fairweather (1991)
Behavioral Research Therapy: Hallahan and Rosenthal (1996)
Bulletin of the Ecological Society of America: Thomas and Krebs (1997)
Canadian Journal of Fisheries and Aquatic Sciences:
Peterman (1989, 1990a)
Conservation Biology: Reed and Blaustein (1995, 1997);
Hayes and Steidl (1997); Thomas (1997)
Ecology: Peterman (1990b)
Journal of Counseling Psychology: Fagley (1985)*Journal of Wildlife Management: (Anon., 1995); Steidl,
Hayes and Schauber (1997)
Marine Pollution Bulletin: Peterman and M’Gonigle (1992)
Neurotoxicology and Teratology: Muller and Benignus (1992)
Rehabilitation Psychology: McAweeney, Forchheimer, and Tate (1997)
Research in the Teaching of English: Daly and Hexamer (1983)
Science: Dayton (1998)
The Compass of Sigma Gamma Epsilon: Smith and Kuhnhenn (1983)
Veterinary Surgery: Markel (1991)
NOTE: ∗ indicates journal requires or requests post-experiment power calculations when test
results are nonsignificant.

Observed power can never fulfill the goals of its advocates because the observed significance level of a test (“pvalue”) also determines the observed power; for any test
the observed power is a 1:1 function of the p value. A
p value is a random variable, P , on [0, 1]. We represent
the cumulative distribution function (cdf) of the p value as
Pr(P ≤ p) = Gδ (p), where δ is the parameter value. Consider a one-sample Z test of the hypothesis H0 : µ ≤ 0 versus Ha : µ > 0 when the√data are from a normal distribution
with known σ. Let δ = nµ/σ. Then Gδ (p) = 1−Φ(Zp −δ),where Zp is the 100(1 − p)th percentile of the standard normal distribution (Hung, O’Neill, Bauer, and Kohne 1997).
That is, Zp is the observed statistic. Both p values and observed power are obtained from Gδ (p). A p value is obtainedby setting µ = 0, so G0 (p) = 1 − Φ(Zp ) = p. Observed
power is obtained by setting the parameter to the observed
statistic and finding the percentile for P < α, so observed
power is given by GZp (α) = 1 − Φ(Zα − Zp ) and thus theobserved power is determined completely by the p value
and therefore adds nothing to the interpretation of results.
An interesting special case occurs when P = α; for theZ test example above it is immediately obvious that observed power = .5 because Zα = Zp . Thus, computing observed power can never lead to a statement such as “because
the null hypothesis could not be rejected and the observed
power was high, the data support the null hypothesis.” Because of the one-to-one relationship between p values andobserved power, nonsignificant p values always correspondto low observed powers (Figure 1). Computing the observed
2

Statistical Practice

power after observing the p value should cause nothing tochange about our interpretation of the p value. These results
are easily extended to two-sided tests.
There is a misconception about the relationship between
observed power and p value in the applied literature which
is likely to confuse nonstatisticians. Goodman and Berlin(1994), Steidl, Hayes, and Schauber (1997), Hayes andSteidl (1997), and Reed and Blaustein (1997) asserted without proof that observed power will always be less than .5
when the test result is nonsignificant. An intuitive counterexample is as follows. In a two-tailed Z test, the test
statistic has the value Z = 1.96 if the test is marginally significant at α = .05. Therefore, the probability of observing
a test statistic above 1.96, if the true mean of Z is 1.96,
is .5. The probability of rejecting the null hypothesis is theprobability of getting a test statistic above 1.96 or below−1.96. Therefore, the probability is slightly larger than .5.
In fact, it is rather easy to produce special examples of test
statistics with skewed distributions that can produce arbitrarily high observed powers for p = α.
A number of authors have noted that observed power may
not be especially useful, but to our knowledge a fatal logicalflaw has gone largely unnoticed. Consider two experimentsthat gave rise to nonrejected null hypotheses. Suppose theobserved power was larger in the first experiment than thesecond. Advocates of observed power would interpret thisto mean that the first experiment gives stronger support favoring the null hypothesis. Their logic is that if power isFigure 1. “Observed” Power as a Function of the p Value for a OneTailed Z Test in Which α is Set to .05. When a test is marginally significant(P = .05) the estimated power is 50%.

low one might have missed detecting a real departure fromthe null hypothesis but if, despite high power, one fails toreject the null hypothesis, then the null is probably true orclose to true. This is easily shown to be nonsense. For example, consider the one-sided Z test described above. Let
Zp1 and Zp2 refer to the observed test statistics in the respective experiments. The observed power was highest in
the first experiment and we know this implies Zp1 > Zp2
because observed power is GZp (α) which is an increasing
function of the Z statistic. So by usual standards of using the p value as statistical evidence, the first experimentgives the stronger support against the null, contradicting
the power interpretation. We will refer to this inappropriate interpretation as the “power approach paradox” (PAP):
higher observed power does not imply stronger evidence
for a null hypothesis that is not rejected.
2.2 “Detectable Effect Size” and “BiologicallySignificant Effect Size”
A second, perhaps more intriguing, application of postexperiment power calculations is finding the hypotheticaltrue difference that would have resulted in a particularpower, say .9. This is an attempt to determine the “detectable effect size.” It is applied as follows: an experimentis performed that fails to reject the null. Then, based on
the observed variability, one computes what the effect size
would have needed to have been to have a power of .9. Advocates of this approach view this “detectable effect size” asan upper bound on the true effect size; that is, because significance was not achieved, nature is unlikely to be near thisstate where power is high. The closer the detectable effectsize is to the null hypothesis of 0, the stronger the evidence
is taken to be for the null. For example, in a one-tailed Z
test of the hypothesis H0 : µ ≤ 0 versus Ha : µ > 0, one
might observe a sample mean X = 1.4 with σX = 1. Thus,
Z = 1.4 and P = .08, which is not significant at α = .05.
We note that if the true value of µ were 3.29 (and σX were
1) we would have power = .95 to reject H0 . Hence, 3.29
would be considered an upper bound on the likely value ofthe true mean. (Note that a 95% upper confidence boundon µ would be 3.04. We return to this point later.)
A variant of the “detectable effect size” approach is the“biologically significant effect size” approach, where one
computes the power at some effect size deemed to be biologically important. The higher the computed power is for
detecting meaningful departures from the null, the stronger
the evidence is taken to be for nature to be near the null
when the null is not rejected.
These inferential approaches have not been justified formally. Cohen (1988, p. 16) claimed that if you design a
study to have high power 1 − β to detect departure ∆ fromthe null hypothesis, and you fail to reject the null hypothesis, then the conclusion that the true parameter value lies
within ∆ units of the null value is “significant at the βlevel. Thus, in using the same logic as that with which we
reject the null hypothesis with risk equal to α, the null hypothesis can be accepted in preference to that which holds
that ES [the effect size] = ∆ with risk equal to β.” (Wehave changed Cohen’s notation in the above to conform tothat used here.) Furthermore, Cohen stated (p. 16) “‘proof’
by statistical induction is probabilistic” without elaboration. He appeared to be making a probabilistic statement
about the true value of the parameter which is invalid in aclassical statistical context. Furthermore, because his procedure chooses the sample size to have a specified, fixed
power before conducting the experiment, his argument assumes that the actual power is equal to the intended powerand, additionally, his procedure ignores the experimental
evidence about effect size and sampling variability because
the value of β is not updated according to the experimental results. Rotenberry and Wiens (1985) and Searcy-Bernal(1994) cited Cohen in justifying their interpretation of postexperiment computed power.
Although many find the detectable effect size and biologically significant effect size approaches more appealing thanthe observed power approach, these approaches also suffer from fatal PAP. Consider the previous two experiments
where the first was closer to significance; that is, Zp1 > Zp2 .
Furthermore, suppose that we observed the same estimatedeffect size in both experiments and the sample sizes were
the same in both. This implies σ1 < σ2 . For some√ desiredlevel of power Πα , one solves Πα = 1−Φ(Zα − nρ/σ) forρ to obtain the desired detectable effect size, ρ. It follows
that the computed detectable effect size will be smaller inthe first experiment. And, for any conjectured effect size,
the computed power will always be higher in the first experiment. These results lead to the nonsensical conclusionthat the first experiment provides the stronger evidence forthe null hypothesis (because the apparent power is higher
but significant results were not obtained), in direct contradiction to the standard interpretation of the experimental
results (p values).
Various suggestions have been made for “improving”
post-experiment power analyses. Some have noted certain
estimates of general effect sizes (e.g., noncentrality parameters) may be biased (Thomas 1997; Gerard, Smith, andWeerakkody 1998), which potentially could be corrected.
Others have addressed the fact that the standard error usedin power calculations is known imprecisely, and have suggested computing confidence intervals for post-experiment
power estimates (Thomas 1997; Thomas and Krebs 1997).
This is curious because, in order to evaluate a test result, one
apparently needs to examine power but, in order to evaluate(test) if power is adequate one does not consider the powerof a test for adequate power. Rather, one switches the inferential framework to one based on confidence intervals.
These suggestions are superfluous in that they do nothing
to correct the fundamental PAP.
3.

POWER ANALYSIS VERSUS CONFIDENCE
INTERVALS

From a pedagogic point of view, it is interesting to compare the inference one would obtain from consideration ofconfidence intervals to that obtained from the power analysis approach. Confidence intervals have at least two interpretations. One interpretation is based on the equivalence
The American Statistician, February 2001, Vol. 55, No. 1

3

of confidence intervals and hypothesis tests. That is, if a
confidence interval does not cover a hypothesized parameter value, then the value is refuted by the observed data.
Conversely, all values covered by the confidence interval
could not be rejected; we refer to these as the set of nonrefuted values. If the nonrefuted states are clustered tightly
about a specific null value, one has confidence that natureis near the null value. If the nonrefuted states range widelyfrom the null, one must obviously be cautious about interpreting the nonrejection as an indication of a “near-null”
state. The more widely known interpretation is that confidence intervals cover the true value with some fixed level ofprobability. Using either interpretation, the breadth of theinterval tells us how confident we can be of the true stateof nature being close to the null.
Once we have constructed a confidence interval, power
calculations yield no additional insights. It is pointless toperform power calculations for hypotheses outside of theconfidence interval because the data have already told usthat these are unlikely values. What about values inside theconfidence interval? We already know that these are values
that are not refuted by the data. It would be a mistake toconclude that the data refute any value within the confidence interval. However, there can be values within a 95%
confidence interval that yield computed powers of nearly.975. Thus, it would be a mistake to interpret a value associated with high power as representing some type of upperbound on the plausible size of the true effect, at least in
any straightforward sense. The proposition that computed
power for effect sizes within a confidence interval can bevery high can be demonstrated as follows. Consider the casewhere the random variable X has a normal distribution. We
wish to test the null hypothesis that the mean is zero versus the alternative that it is not zero. A random sample oflarge size is taken which has a mean, x, of 2 and a standard
error of the mean of 1.0255. The upper critical region fora two-sided Z test then corresponds to values of the mean
greater than 1.96 × 1.0255 = 2.01. Therefore, we fail to reject the null hypothesis. A 95% confidence interval wouldbe (−.01, 4.01). We note that a value of 4 for the population mean is not refuted by the data. Now post-hoc power
calculation indicates the probability of rejecting the null
hypothesis if the mean is actually 4 is Pr(|X| > 2.01) =Pr(Z > (2.01 − 4)/1.0255) + Pr(Z < (−2.01 − 4)/1.0255)
which is about .974. Thus, the power calculation suggeststhat a value of 4 for the mean is unlikely—otherwise weought to have rejected the null hypothesis. This contradicts
the standard theory of hypothesis tests.
4.

EQUIVALENCE TESTING

Simply saying that an experiment demonstrates that atreatment is “near-null” because the confidence interval
is narrow about the null value may seem unsatisfactorily“seat-of-the-pants.” However, this can be formulated as arigorous test. Suppose that we are willing to conclude thata treatment is negligible if its absolute effect is no greaterthan some small positive value ∆. Demonstrating such practical equivalence requires reversing the traditional burden
4

Statistical Practiceof proof; it is not sufficient to simply fail to show a difference, one must be fairly certain that a large difference
does not exist. Thus, in contrast to the traditional castingof the null hypothesis, the null hypothesis becomes that atreatment has a large effect, or H0 : |D| ≥ ∆, where D isthe actual treatment effect. The alternative hypothesis is the
hypothesis of practical equivalence, or HA : |D| < ∆.
Schuirmann (1987) showed that if a 1 − 2α confidence
interval lies entirely between −∆ and ∆, we can reject thenull hypothesis of nonequivalence in favor of equivalenceat the α level. The equivalence test is at the α level because
it involves two one-tailed α level tests, which together describe a 1 − 2α level confidence interval. This approach toequivalence testing is actually always a bit on the conservative side; the actual level α0 for normally distributed datafrom a one-sample experiment√ with known σ and nominal
level α is α0 = α − 1 + Φ (2∆ n/σ − Zα ), which shows theconservatism√ will be slight in many practical applications
where 2∆ n/σ substantially exceeds Zα . More powerfulequivalence testing procedures exist (e.g., Berger and Hsu
1996), but for well-behaved problems with simple structures the simplicity of this approach seems to make it acompelling choice to recommend to the researcher involvedin analysis (Hauck and Anderson 1996).
Considering the power approach as a formal test in theabove equivalence testing framework makes it clear why
it is logically doomed. The power approach requires twooutcomes before declaring equivalence, which are (1) thenull hypothesis of no difference H0 : D = 0 cannot be rejected, and (2) some predetermined level of power must be
achieved for |D| = ∆. To achieve outcome 1, the absolutevalue of the observed test statistic must be less than Zα .
This in turn implies that the√ observed absolute differenceσ/n. Thus, as |D| becomes more|d| must be less than Za
precisely estimated by increasing n or decreasing σ, the observed difference |d| must become progressively smaller if
we want to demonstrate equivalence. This simply does notmake sense: it should become easier, not more difficult, toconclude equivalence as |D| becomes better characterized.
Schuirmann (1987) noted that when viewed as a formal testof equivalence, the power approach results in a critical region that is essentially upside down from what a reasonableequivalence test should have.
5.

DISCUSSION

Because of the prominence of post-hoc power calculations for data analysis in the literature, elementary statistics texts should devote some attention to explaining whatshould not be done. However, there is a larger lesson to belearned from the confusion about power analysis. We believe the central focus of good data analysis should be tofind which parameter values are supported by the data andwhich are not. Perhaps unwittingly, advocates of post-hoc
power analysis are seemingly grappling with exactly thisquestion.
The reader with Bayesian inclinations would probably
think “what foolishness—the whole issue would be moot if
people just focused on the sensible task of obtaining poste-

rior distributions.” Philosophically, we find this attractive as
it avoids some nagging issues in frequentist statistics concerning p values and confidence intervals (e.g., Berry 1993;
Freeman 1993; Schervish 1996; Goodman 1999a,b). But,
the real world of data analysis is for the most part solidly
frequentist and will remain so into the foreseeable future.
Within the limitations of the frequentist framework, it isimportant that analyses be as appropriate as possible.
Introductory statistics classes can focus on characterizing which parameter values are supported by the data byemphasizing confidence intervals more and placing less emphasis on hypothesis testing. One might argue that a rigorous understanding of confidence intervals requires a rigorous understanding of hypothesis testing and p values. We
feel that researchers often do not need a rigorous understanding of confidence intervals to use them to good advantage. Although we cannot demonstrate it formally, we
suspect that imperfectly understood confidence intervals are
more useful and less dangerous than imperfectly understood p values and hypothesis tests. For example, it is surely
prevalent that researchers interpret confidence intervals as
if they were Bayesian credibility regions; to what extent
does this lead to serious practical problems? The indirect
logic of frequentist hypothesis testing is simply nonintuitiveand hard for most people to understand (Berry 1993; Freeman 1993; Goodman 1999a,b). If informally motivated confidence intervals lead to better science than rigorously motivated hypothesis testing, then perhaps the rigor normallypresented to students destined to be applied researchers canbe sacrificed.
Of course, researchers must be exposed to hypothesis
tests and p values in their statistical education if for noother reason than so they are able to read their literatures.
However, more emphasis should be placed on general principles and less emphasis on mechanics. Typically, almost
no attention is given to why a particular null hypothesis
is chosen and there is virtually no consideration of otheroptions. As Hauck and Anderson (1996) noted, both statisticians and nonstatisticians often test the wrong hypothesis
because they are so conditioned to test null hypotheses of
no difference. Statisticians need to be careful not to present
statistical analysis as a rote process. Introductory statistics
students frequently ask the question, “why focus on protection against erroneously rejecting a true null of no difference?” The stock answer is often something like “it isbad for science to conclude a difference exists when it doesnot.” This is not sufficient. In matters of public health andregulation, it is often more important to be protected against
erroneously concluding no difference exists when one does.
In any particular analysis, one needs to ask whether it ismore appropriate to use the no difference null hypothesis
rather than the nonequivalence null hypothesis. This is aquestion that regulators, researchers, and statisticians need
to be asked and be asking constantly. We doubt whether
many researchers are even aware that they have choiceswith respect to the null hypotheses they test and that the
choices reflect where the burden of proof is placed.
We would not entirely rule out the use of power-type concepts in data analysis, but their application is extremely lim-

ited. One potential application might be to examine whether
several experiments were similar, except for sample size;
this might be an issue for example in meta-analyses (Hung,
O’Neill, Bauer, and Kohne 1997). The goal here, examining homogeneity, differs from the usual motivations for post
hoc power considerations.
Power calculations tell us how well we might be able tocharacterize nature in the future given a particular state andstatistical study design, but they cannot use information in
the data to tell us about the likely states of nature. With
traditional frequentist statistics, this is best achieved withconfidence intervals, appropriate choices of null hypotheses,
and equivalence testing. Confusion about these issues could
be reduced if introductory statistics classes for researchers
placed more emphasis on these concepts and less emphasison hypothesis testing.
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