Statistical power — where it appears
Named by 56 essays across 31 fields — each of them below, with the objects they name alongside it.
Choosing n after looking
Re-estimating the sample size from an interim is the one adaptation with a defence, and the defence is exactly what it costs: an analyst kept blind to the arms measures a spread that contains the effect, so the design overshoots by 1 + Δ²/4σ². Re-estimating the effect instead breaks the error rate.
Not half and half
The same units, the same measurements, the same analysis — and a different variance, decided before anything is measured. When the two arms have different spreads the best split is σ₁ : σ₂, equal allocation costs 2(σ₁²+σ₂²)/(σ₁+σ₂)², and at three to one that is a quarter of the experiment.
The design that cannot see a curve
A two-level factorial has every run at a corner, where every squared term equals one — so the column that would estimate curvature is a copy of the intercept, and the design has no information about it at all. A few runs at the centre buy one number back, and only one.
The spread a pilot supplies
A trial sized for 80% power from a pilot's standard deviation is sized from an estimate that is too small more often than not. With a pilot of ten, 55.9% of the trials it sizes have less than 80% power and 11.1% less than 50%, although the planned sample is right on average. Sizing from the pilot's 80% upper confidence limit instead leaves 19.8% short, at 1.65 times the sample; from its 90% limit, 10.0% short at 2.12 times.
Five times in six
A 95% interval is read as a 95% chance that a replication's estimate will land inside it. With the spread known and a replication of the same size, the chance is 83.42% — five times in six — because both estimates are uncertain. An original that landed two standard errors from the truth captures a replication 48.40% of the time; a replication a tenth the size lands inside 44.54% of the time; and among significant originals from studies with 17% power, 66.94%.
A probe nobody chose
On a set that is definitively in two pieces, seven of twenty-four outcomes report nothing at all. Every covariate probe reports it. What separates them is not accuracy — it is that one of them can be chosen and the other is what happened.
A taper and a critical value
Two constructions whose tapers visibly differ give the same critical value, and two that share a taper exactly do not. Adding a construction whose taper is a decision rather than an accident says which half of that is true.
Randomising towards the winner
Allocating more patients to the arm that is doing better is the humane thing to want and it buys nothing statistically: at a fixed total it costs thirty points of power. And because the allocation is a function of the outcomes, the ordinary test on it rejects a true null 7.8% of the time before any time trend is applied — and 58% after one.
The charge that is not a sum
Charging two searches what each costs on its own is conservative, and conservative here means the test never fires. At the largest break measured it declares nothing, on every draw, while a calibrated threshold reaches 29%.
What a p-value does not say
The same p of 0.04 corresponds to a large effect in ten observations and a negligible one in two thousand. A p-value alone cannot be interpreted, and the number that makes it interpretable is almost never printed beside it.
When one model contains the other
The comparison a forecaster most often wants is between a model and the same model with one more term. That is exactly the comparison the standard test cannot make — and it fails by declaring the smaller model significantly better, more confidently the more data it is given.
The two worlds that look the same
Three causal structures were fitted to one covariance matrix and agree with it to 4.4·10⁻¹⁶. The regression returns 0.5000 under all three; the effect they hold is 0.5000, 0.8481 and 0.8481. What separates structures is a missing edge, and the signature of one is a correlation of exactly zero.
What naming it in advance costs
Preregistration is argued for as free. Against an effect of two standard errors hiding in one of twenty analyses, naming the right one detects it 51.5% of the time and naming the wrong one detects it 4.7% of the time; correcting all twenty detects it 22.5% wherever it is. The two are worth the same when the chance of having named correctly is 38%.
Two intervals that overlap
Two 95% intervals that just touch are read as a difference at the edge of significance. With equal standard errors their difference has p = 0.0056, not 0.05; two intervals can overlap by 58.6% of an arm and still differ at exactly 5%; standard-error bars that just touch mark p = 0.157; and when the two estimates are correlated at 0.8, touching intervals conceal a difference of 6.2 standard errors. Read as a test, non-overlap needs 1.66 times the sample for the same power.
The chance a trial succeeds
A trial of sixty-four per arm has 80% power at an effect of half a standard deviation. If the effect is only believed to be about half a standard deviation, give or take a quarter, the chance the trial reaches significance is 69.2%; give or take a half, 61.4%. Reaching 80% then takes 113 per arm, or 1,268 — and when the belief is uncertain by three quarters of a standard deviation no number of patients reaches 80%, because the chance can never exceed the 74.8% probability that the effect is positive at all.
One control, many arms
The control appears in every comparison, so it is worth √k treatment arms — and the same sharing makes the k tests correlated at n/(n+n₀), which is the quantity Bonferroni ignores. Both facts come out of one design decision, and it is the size of the control.
The analysis after three arms
An unadjusted analysis after a two-arm balancing rule rejects 0.6% of true nulls where it claims 5%. With three arms and a deterministic rule it rejects none at all — and the repair is the same repair, which is a sentence and a column in the model.
The analysis has to know the rule
A trial balanced by minimisation and analysed by comparing the two arms' means rejects a true null 0.6% of the time where it claims 5%, and at full determinism 0.0%. That is not an error anybody complains about — it is a test that has stopped working, paid for by a balance the analysis then refused to use.
The models that were never in the running
A reference distribution for a set has to assume something about every candidate in it. Assuming that all of them are as good as the benchmark is what makes the reality check honest, and it is what sixteen hopeless candidates use to destroy it.
The price of control
Every correction is paid for in power, and the exchange rate can be measured. Holm buys familywise control for 33 percentage points of power; Benjamini–Hochberg buys a weaker guarantee for 10. Neither is free and neither is a matter of taste.
The winner's curse
Filter honest studies down to the ones that reached significance and the effects they report are systematically too large. At low power the inflation is a factor of two, nobody has done anything wrong, and the selection did all of it.
What a chosen probe finds
On a chain of eight hundred draws the probe the earlier fields use misses 44% of the sets that are split. Its own residual off the rule's span misses 12%, for one least-squares fit.
What the balanced trial is worth
A rule that reads the covariate removes three quarters of the imbalance. An analysis that does not know it happened prices the imbalance anyway, rejects one true null in two hundred instead of one in twenty, and finds a real effect less often than a coin-tossed trial does.
A coverage table with its own error
Twenty cells estimating the coverage of an interval that is exactly 95%, at a thousand replications each, read from 93.9% to 96.5% — and a table like that flags at least one of its correct cells on 69.9% of honest runs. Ten times the replications does not repair it: at ten thousand the same table still flags one 63.3% of the time.
The effect a stopped trial reports
An O'Brien–Fleming trial at 88.45% power holds its error rate exactly and reports an effect 9.6% too large on average. The 11.39% of trials that stop at the second look report 1.83 times the truth, the ones that cross at the last look report 0.80 times it, and pooling every trial by its size gives the truth back to the last digit.
The correction that makes the estimate worse
Correcting for twenty analyses repairs the p-value by demanding a larger statistic, and a larger statistic is a more selected one. At two standard errors the surviving estimate averages 1.35 times the truth before the correction and 1.69 times it after — so the honest error rate is bought with a more inflated effect.
Significant in one, not in the other
Two studies of exactly the same effect, each with 50% power, disagree about significance half the time — and when they do, the test of the difference between them is significant in 9.75% of cases. A p of 0.01 beside a p of 0.20 is a difference with p = 0.36. Among four subgroups sharing one effect, at least one significant and one not happens 87.5% of the time, and the test that would tell a real difference apart needs four times the sample the effect itself needed.
An outcome cut in two
Replacing a measured outcome with whether it crossed a threshold keeps 63.7% of the information when the cut is at the mean, 34.2% at the top tenth and 13.1% two standard deviations out. A trial that needs 63 patients per arm on the measured outcome needs 102 cut at the mean and 185 cut at one and a half standard deviations. The responder rates that result read as a share of patients who respond — 50.0% against 69.1% — when every patient moved by the same amount; and a cut chosen after looking turns a 5% test into a 17.7% one.
A distribution drawn from the null
Between nested models the ordinary comparison statistic has a null distribution centred at minus one and a 95% point of a quarter. A correction to its mean repairs the centre and leaves the shape; simulating the null repairs both.
How many subjects
Sixty-four per arm for 80% power at half a standard deviation — a power figure that could only be simulated, with nothing to disagree with, until the non-central t was written. Two routes now, agreeing to within the simulation's own error.
The check before the standard error
One number decides whether every interval in an analysis is trustworthy, and the check for it flags a lag-one correlation of 0.5 nine times in ten — and one of 0.2 only one time in five, where the interval already covers 88.6% instead of 95%.
The corner the test is calibrated at
"No candidate is better than the benchmark" is not a null but a face of a region, and a reality check is calibrated at one corner of it. Fill the table with candidates that are hopeless rather than equal and the test finds a genuine improvement 0.0% of the time.
The reference the covariates supply
Hold the outcomes fixed, re-run the rule that assigned them, count. The same construction cost nineteen points of power in the adaptive field, because its rule chased outcomes and its critical value depended on a rate nobody has. Here the rule reads only what was recorded before anything happened, and the same unadjusted statistic goes from 20.3% power to 55.0% by being read against the right distribution.
What the exactness buys
Against a z test calibrated to reject exactly 5% of true nulls on this design, the randomisation test loses nineteen points of power. What it buys is that the calibration needs the success rate — which moves the critical value from 1.668 to 2.718 and is the quantity the trial was run to find out.
When the constraints run out
Every function added to a basis is a constraint the assignment has to satisfy with the same units. At sixteen units and a stated tolerance the admissible assignments run 3,874, then 1,006, then 314, then none — and the count is exact, because the assignment space is finite.
False discoveries that arrive together
Correlate twenty tests and Benjamini–Hochberg still holds its false discovery rate — 1.66% at a correlation of 0.9 with ten real effects, against 2.55% when the tests are independent. What changes is how the errors come. A family of true nulls reports anything 2.34% of the time instead of 5.08%, and when it does, it reports 16.56 false findings out of twenty.
Two instruments that disagree
The overidentification test keeps its size at 5.0% and reaches 86.4% power against a violation carried by one instrument. Against the same error carried by both in proportion to their first stages it rejects on 4.6% of draws — its own size — while the estimate is wrong by 0.3000, which is 94.2% of the confounding the instruments were brought in to remove.
When the order matters
Three ways of breaking exchangeability cost 4.93, 11.07 and 1.07 points of coverage, and the ordering by cost is the reverse of the ordering by how soon a test would have caught them. The departure practitioners check for is the cheapest one.
Right for the wrong reason
A robust standard error costs no coverage where the risk is absent — 95.52% against 95.06% at twenty rows. It costs a 6.89% wider interval and a variance estimate 2.572 times as variable, and the pre-test that would avoid paying recovers 15.9% of what the insurance is worth.
The miscalibration a perfect forecaster shows
A forecaster whose true reliability is exactly zero shows a calibration error of 0.1252 on fifty forecasts and 0.0090 on ten thousand. Every one of 1,200 blameless hundred-forecast records exceeds the 0.02 routinely read as evidence of a problem, and the mean does not fall under it until 1,976 forecasts.
The p-value a replication gets
Under a true null a p-value is flat. Under a real effect its distribution is closed form and wide — a study with 80% power returns anything from 4.4×10⁻⁵ to 0.13 in eight runs of ten — and the chance that an exact replication of a p = 0.05 result is significant again is exactly one half, under both of the models people use without naming them.
A simulation that stops when it looks settled
A simulation of an interval that covers exactly 95%, checked every 250 replications for a significant departure and stopped when it finds one, flags that correct interval on 29.54% of runs. Stopped instead as soon as its estimate reaches 95%, it reports an interval that covers 94% as meeting its level on 37.21% of runs. Stopped when the estimate stops moving, it reports the right number — and has quietly chosen to run about fifteen hundred replications.
A boundary for giving up
Adding "stop if z is below zero" to an O'Brien–Fleming trial costs 5.20 points of power at the effect it was designed for and halves the observations a trial with no effect uses. Stopping when conditional power at the observed trend falls under 10% costs 13.23 points and stops 21.28% of trials with a real effect. Making that rule binding lowers the benefit boundary from 2.040 to 1.901, and a binding rule that is then ignored rejects a true null 3.523% of the time instead of 2.5%.
Estimating how many nulls are true
Benjamini–Hochberg at 5% delivers 2.55% when half of twenty nulls are false, because it cannot tell how many are. Storey's estimate of that share, read off the p-values above one half, spends the rest and finds 81.93% of the real effects instead of 74.70% on independent tests. Correlated at 0.9, the same procedure reports a finding in 19.29% of families in which every null is true.
The cliff that is a slope
A regression between two independent series is called significant 4.9% of the time at no persistence, 52.4% at a lag-one correlation of 0.9, and 83.4% at a unit root. The rule the field offers asks whether the last of those holds, and at 0.9 the unit-root test correctly refuses one 87.2% of the time.
The rank is a decision
The sequential procedure's 5% bounds one of its two errors. Over-counting reads between 4.2% and 7.2% at every sample length from fifty observations to three hundred; under-counting reads 69.5% at fifty and 0.0% at three hundred, and nothing in the procedure bounds it.
The hazard ratio the follow-up chose
A treatment that halves the hazard for one year and then does nothing has a Cox hazard ratio of 0.5000 if the trial stops at one year, 0.7617 at three and 0.8194 at eight. Nothing about the treatment differs between those numbers. When hazards are not proportional the hazard ratio is an average, and the length of follow-up and the dropout rate choose its weights.
Two ways to combine p-values
Fisher's and Stouffer's combinations are both exactly right when every null is true, for the single reason that each p-value is flat. Under a real effect they disagree about which evidence counts: with Stouffer held at 50% power across ten studies, Fisher is the more powerful while the signal sits in six or fewer of them and the less powerful from seven.
A look the trend asked for
Under an O'Brien–Fleming-type spending function, every schedule of looks fixed in advance spends exactly 5.0000%. A committee that adds a look at three quarters of the trial whenever the interim z is 1.5 or more spends 5.2323% — 5.315% counted over a hundred thousand trials — and the most a committee choosing among six schedules could spend is 5.4390%.
An order that spends the error rate
Test twenty hypotheses in a declared order, each at the full 5% and each only if every one before it was rejected, and the first is found 85.3% of the time where Holm finds it 52.5%. The tenth is found 20.4% of the time, the product of the powers before it. Move one true null to the head of the list and every real effect behind it is found no more than 4.3% of the time.
The repair that keeps the question
A regression between two independent trending series is significant 82.9% of the time on random walks and 100.0% on trend-stationary ones. Subtracting a fitted line leaves 74.2% and 33.5%; differencing leaves 5.0% and 5.2% and throws away the trend the study was about.
A statistic that is exact twice
Dividing the difference in means by its own separate-variance standard error before permuting takes the rejection rate under a true weak null from 20.47% to 6.07%, keeps the exactness under the sharp null at 4.07%, and costs 0.8 points of power against a real effect. At an even split it changes nothing at all, in every draw.
The smallest of three combinations
Reporting whichever of Fisher's, Stouffer's and Tippett's combinations is smallest is a test of its own, and on ten studies of nothing it rejects 9.66% of the time — not 5%, and nowhere near the 15% the three sizes add to, because the statistics are correlated at up to 0.903. Read at 2.448% each it is exact, and then it trails the best single combination by at most 7.45 points and leads the worst by at least 10.30.
A horizon chosen after looking
A difference in restricted mean survival read at whichever of eleven horizons looks most convincing rejects 11.24% of trials in which the treatment does nothing, against 4.70% at a horizon fixed in advance. The correlation of the differences across horizons is closed, and the Gaussian process it defines prices the choice at a critical value of 2.317 — which brings the counted size back to 4.99% and keeps 96.92% of the power that a horizon nobody could have known to fix would have had.
How slow a return a sample can see
At two hundred observations the test finds a gap that halves in five steps four times in five, one that halves in eight 37.3% of the time, and one that halves in fifty 4.95% of the time — which is the rate at which it finds pairs with no mechanism at all. The boundary moves with the sample, not with its square root.
A detector built for the ordering
The best of three checks for a drifting scale fires at half the growth factor the standard one needs — 2.12 against 4.31 — and still leaves 6.50 points of coverage gone before it does, against 0.51 for serial correlation. The reversal was not a property of the test.
Named alongside it
The objects these essays reach for when they reach for this one.
Monte CarloError rateSample sizeMultiple comparisonsReference distributionp-valueCritical valueClosed formNull hypothesisEffect sizeRandomisation testCoverage