Normal Distribution
nothing is called 95% until it has been counted
Concept

Error rate — where it appears

How often a procedure makes a stated kind of mistake over the experiments it might have been run in. Which rate a procedure controls is a choice, and a procedure that controls one says nothing at all about another.

Named by 47 essays across 24 fields — each of them below, with the objects they name alongside it.

What the interim sees, at an effect of 1. The same 60 observations, estimated two ways. Keeping the arms separate gives 0.995, which is σ. Pooling them without separating the arms — the price of staying blind to the comparison — gives 1.114, against the identity √(1 + Δ²/4σ²) = 1.118. The sample size is proportional to the variance, so a blinded design at this effect asks for 25% more units than it needs, and it does so systematically rather than by chance.

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.

adaptive · Stopping The allocations the rule could have made, from these exact patients. One 200-patient trial allocated by response-adaptive randomisation, re-randomised 999 times. No outcome is redrawn anywhere in this figure: each re-randomisation runs the same rule over the same patients in the same order, so what is drawn is the set of experiments that could have happened rather than a sampling distribution. The observed |z| is 1.417, 258 of the 999 re-randomisations reach it, and the p-value is (1 + 258)/(1 + 999) = 0.2590. The curve is the half-normal the ordinary analysis reads the same statistic against; its 5% point is 1.96 and this distribution's is 2.101.

The experiments that could have happened

An adaptive trial's allocation is a function of the outcomes it will later be compared against, so the ordinary analysis rejects a true null 9.2% of the time. Hold the outcomes fixed, re-run the rule that assigned them, and count — the same statistic against a reference distribution the trial could actually have drawn from is back at 4.0%.

exact · Reference Three quantities, and only one of them crosses zero. Two forecasts of an AR(1) — the last value carried forward and the mean of the last 60 observations — at 1 step ahead. The curve through zero is σ₁² − σ₂², the difference in expected squared error that a comparison of accuracy tests; it changes sign at φ = 0.4922. The two curves above it are σ₁² − σ₁₂ and σ₂² − σ₁₂, the quantities the two encompassing tests are about, and neither of them comes near zero anywhere: the smallest value either takes across the range is 0.008 times the variance of the series. All three are closed forms in φ, R and h with no simulation in them. Equal accuracy is one hypothesis about this picture and encompassing is another, and a set of numbers can satisfy either without the other.

What the other forecast adds

Two forecasters, one series, and two different questions about them. Which is more accurate has an answer that changes with the persistence of the series; whether either is redundant has an answer that never changes at all.

ranking · Forecast One true null, one table, five readings. every subset of four, fifteen models, at a null where nothing any candidate holds is worth anything, over 500 draws. Each bar is the share of draws on which that reading declares a difference at a nominal 5%. The reading is the whole of the difference between the bars: the data is identical. An open search over all 210 ordered pairs rejects 76.2%; the table's own 5% point is 3.163 against the 1.671 a single comparison uses. Bonferroni takes the open reading to 0.6% — and on the nested ladder the same correction does not reach the nominal level at all, because there the excess is a shift in the mean rather than a maximum over many.

When the benchmark is a candidate

A specification search with a benchmark nailed down is the case with a closed form. Take the nail out — let the model that would have been reported be one of sixteen, chosen by the same data as its rivals — and the same true null is read three ways, at 2.0%, 7.8% and 76.2%.

select · Forecast Testing at 0.05 every time the data is looked at. The null is true in every one of these trials and the test is correct every time it is run. Looking once rejects 4.9% of the time, as it should; looking ten times rejects 19.2% of the time. Nothing changed except permission to look.

When the looking happens

A p-value is defined relative to a sampling plan, so the same data means different things under different stopping rules. Testing five times at the nominal level rejects a true null 14% of the time, and no observation in the dataset changed.

sequential · Stopping One comparison, and the two error bars it can be given. 60 rolling origins, a window of 60 observations, forecasts 4 steps ahead, at the persistence φ = 0.8256 where the two benchmarks have exactly equal population mean squared error. Each mark is one origin's difference in squared error; the horizontal line is their mean, 0.6522. The two vertical bars at the right are ±1.96 standard errors round that mean computed two ways — 0.5337 treating the differences as independent, 0.6880 allowing for the overlap between neighbouring forecasts. The null is true here by construction, so an interval that excludes zero is a mistake, and the narrow one does it far more often than the wide one.

Which forecast is better

Two forecasters, one series, and a difference in mean squared error. Whether that difference is real is a hypothesis test, its terms are not independent, and the standard error it needs is not the one a t-test computes.

evaluation · Forecast How far each reference distribution's 95% point falls short. Seven constructions on rows that repeat each other, at a block length of 5 and 200 draws, against the statistic's own 95% point of 3.0224 computed from three thousand draws of the same world. Reading down: a multiplier on every row keeps no dependence at all and is 44% short; a multiplier shared along a block keeps the triangle; a fixed block keeps the same triangle and is 8% closer, which is the pair that says a taper is not what decides this; the stationary bootstrap; the two tapered blocks, both further short than the untapered one at this block length; and errors generated from a fitted model, which is the only construction here not bounded by what the residuals report.

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.

taper · Reference Eight candidates, one of them exactly as good as the benchmark. The candidate set: moving averages of the last 1, 2, 3, 5, 8, 13, 21 and 34 observations, each drawn as its expected squared error divided by the benchmark's — the mean of all 60. The persistence is not chosen, it is solved for: at φ = 0.4895 the best candidate in the set, the average of 2, has exactly the benchmark's expected squared error, and every other candidate is worse by between 0.5% and 5.1%. So the null that no candidate beats the benchmark is true, with one candidate on its boundary. Everything a set comparison claims about its own error rate has to be measured here, because anywhere further inside the null every procedure flatters itself.

Eight forecasters and one benchmark

A set of forecasters is a multiplicity problem on top of a dependence problem, and the two do not separate. Eight windows of one series carry the multiplicity of two and a half independent comparisons; eight separate problems carry eight.

ranking · Multiplicity Every way of splitting 16 units into two halves. All 12,870 assignments, enumerated. The spread of the standardised imbalance is exactly 2/√n = 0.500, whatever the covariate's own distribution, and 33.3% of assignments differ by more than 0.5 standard deviations. Randomisation does not deliver balance; it delivers a known distribution of imbalance.

Randomisation is not balance

A third of all ways to split sixteen units leave the two halves more than half a standard deviation apart on a covariate. What randomisation delivers is not balance but a known reference distribution — and it makes a test exact with no assumption about the data's shape at all.

design · Randomisation 20 adaptive trials, 45% against 25%. Each line is one trial allocating patients one at a time by the arm's own posterior. The average final share on the better arm is 84.7%, with a standard deviation of 10.3 points across these 20 trials. The rule does not deliver a fixed advantage: it delivers one that depends on how the first few patients came out.

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.

adaptive · Randomisation Four boundaries for 5 looks, all spending 5% in total. test at 0.05 every look: 1.96, 1.96, 1.96, 1.96, 1.96. Pocock — a constant, higher boundary: 2.41, 2.41, 2.41, 2.41, 2.41. O'Brien–Fleming — strict early, nearly nominal at the end: 4.55, 3.22, 2.63, 2.27, 2.03. Bonferroni across looks: 2.58, 2.58, 2.58, 2.58, 2.58. Every one except the first spends the same total error rate; they differ in when they spend it.

Spending the error rate

The repair for interim testing is to spend 5% across the looks rather than at each one. The boundaries are solvable rather than quotable, and a trial that can stop early uses 298 observations where a fixed design uses 400 — at a cost of half a point of power.

sequential · Stopping The allocations the rule could have made, from these exact patients. One 200-patient trial allocated by response-adaptive randomisation, re-randomised 999 times. No outcome is redrawn anywhere in this figure: each re-randomisation runs a fair coin rule over the same patients in the same order, so what is drawn is the set of experiments that could have happened rather than a sampling distribution. The observed |z| is 1.417, 155 of the 999 re-randomisations reach it, and the p-value is (1 + 155)/(1 + 999) = 0.1560. The curve is the half-normal the ordinary analysis reads the same statistic against; its 5% point is 1.96 and this distribution's is 1.946.

The test that needs the rule

A randomisation test assumes almost nothing about the data and one thing about the experiment. Tell it a fair coin produced an allocation that an adaptive rule produced — which is what every off-the-shelf permutation routine does — and it rejects 8.0% of true nulls where knowing the rule gives 4.0%.

exact · Reference Where the residual test's statistic actually falls, at n = 200. Four thousand pairs of unrelated random walks, each regressed on the other and each residual tested for a unit root. The statistic is computed as a t and its distribution is not a t: five per cent of it falls below -3.38, where the ordinary one-sided 5% point of a t on 198 degrees of freedom is -1.65. Everything left of -1.65 — 70.2% of the whole distribution — is a pair of unrelated walks that a t table calls cointegrated.

The test with no table

The statistic that separates a real long-run relation from a spurious one is computed as a t and is not a t. At two hundred observations its 5% point is −3.38 where the t table says −1.65, and reading it against the table calls two unrelated random walks cointegrated 70.5% of the time.

cointegration · Spurious Twenty tests, 10 of them real — what each procedure holds. no correction: familywise 40.8%, false discovery 5.3%, power 85%. Bonferroni: familywise 2.8%, false discovery 0.5%, power 49%. Holm: familywise 3.6%, false discovery 0.6%, power 53%. Benjamini–Hochberg: familywise 20.0%, false discovery 2.6%, power 75%.

Two different promises

Bonferroni bounds the chance of any false positive. Benjamini–Hochberg bounds the share of the findings that are false. Both are called correcting for multiple comparisons, and one of them lets the familywise rate reach 20%.

multiplicity · Multiplicity A test between nested models, under a null that is true. 1000 comparisons: an AR(1) truth, forecast by a fitted AR(1) and by a fitted AR4 whose extra coefficients are zero. In population the two forecasts are identical, so every rejection is false. The larger model's mean squared error is 1.1663 against 1.0583 — worse, by exactly the noise in estimating coefficients that are not there — and the ordinary test therefore declares the smaller model significantly better 67.2% of the time. Read one-sided in the direction anybody asks about, it finds the larger model better 0.0% of the time. Adding the squared difference between the two forecasts back into the loss differential puts the level at 4.9%.

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.

evaluation · Forecast The pooled two-sample test's size, with a true null everywhere. Forty units split between two groups, with the second group's variance a stated multiple of the first's, and the two population means equal. A 5% test should reject 5% of the time. The pooled test runs from 0.55% to 18.91% across this region; Welch's runs from 4.63% to 5.51%.

A degrees of freedom that is not a count

The pooled two-sample test's size runs from 0.55% to 18.91% across forty units split five ways against five variance ratios, with a true null in every cell. Welch's runs from 4.63% to 5.51% — bought with a degrees of freedom that is a function of the data, not an integer, and not a count of anything.

tails · Student How often the split is taken, and by which rule. Over 400 draws on each of five laws. The first two rows have no break in them at all, the last two have one at row 60, and the middle one is a moving average. A criterion that counts a fitted two-regime model's parameters and nothing else takes the split on 99% of draws where there is no break. Counting the break point as one more parameter brings that to 67%. Charging what the search actually manufactures — 5.16 units, measured on a law with no break — brings it to 16%, and still takes the split on 61% of draws where there is one.

Choosing whether to break

Charging what the search manufactures takes a rule from splitting a stationary sample on 99% of draws to 16%. It also costs regret, because the two mistakes a rule can make are not the same size.

charged · Break point The trace statistic under the null, and the 5% point it needs. 600 systems of 3 unrelated random walks, each put through the reduced-rank regression, with the statistic for "rank ≤ 0" collected. The 5% point is 31.91. There is no standard table to look that up in: the distribution depends on the number of common trends under the null and is not a chi-square, so the value is simulated on one set of seeds and applied on another — exactly the position the pair's residual test was in one field ago.

Counting what is still wandering

The statistic that turns a spectrum into an integer has one name and three distributions. Its 5% point is 8.12, 18.64 or 31.74 depending only on how many series are left wandering under the null being tested — and read against the wrong one of those three, it calls unrelated random walks cointegrated most of the time.

systems · Rank The best of 8 arms, tested as though it were the only one. 8,000 trials with no effect in any arm. Stage one runs 8 arms at 60 each, the best is carried forward, and stage two adds 30 more to it and to the control. The histogram is where the final statistic lands and the curve is the standard normal it is being read against — shifted right, because the arm was chosen for being ahead. 10.5% of these trials clear 1.96 against a claimed 5%, and the value that actually holds the rate for this design is 2.313.

Dropping the losers

Carrying the best of eight arms forward and testing it at 1.96 rejects a true null 10.3% of the time — the hypothesis was chosen by looking at the data, so the statistic is a maximum wearing a single comparison's clothes. The value that holds the rate is 2.313, and it has to be solved for.

adaptive · Stopping Which repair goes with which defect. The share of true nulls rejected at a nominal 5% by a reference distribution generated from the fitted benchmark, over 120 draws with 59 resamples each. Where the errors are well behaved every resampling is fine and all four are conservative. Where the variance is a function of the design, the two that detach a residual from its own row reject 5.8% and 8.3% — and the block bootstrap, which is the resampling three earlier fields on this site reach for, repairs nothing at all, because the dependence it is built for is between origins and the rolling scheme reproduces that on its own. Where the errors are skewed the symmetric multiplier is the one that is wrong, and Mammen's two-point version is the only one of the four that is right in both columns.

Residuals that keep their own variance

A reference distribution for a search has to be generated from a fitted model, and the generator draws residuals. Four ways of drawing them keep four different things — and the one this site has reached for three times repairs nothing at all here.

select · Bootstrap Four analyses of the same 3-arm trials, under a true null. 250 trials of 150 patients, 3 arms, minimisation with p = 0.85, 99 re-randomisations for each exact test. Two statistics — an F on the arms alone and an F on the arms after the balanced factors — against two reference distributions: the table the statistic is named for, and the distribution the allocation rule itself generates when the outcomes are held fixed and the rule is re-run. Only the first cell is wrong, and it is wrong in the direction that costs power rather than the one that manufactures findings: 0.0% where 5% is claimed. Either repair works — adjusting for what the rule balanced, or asking the rule what it would have done.

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.

multiarm · Assignment Four analyses of the same trials, with no treatment effect at all. 700 trials of 120 patients allocated by minimisation at p = 0.8, with the prognostic factors carrying a real effect on the outcome and no treatment effect — every rejection below is a false one. Two statistics, the plain difference and the same after adjusting for the balanced factors, each read against two reference distributions: a t table, and the set of allocations the rule could have produced from these covariates. The unadjusted comparison rejects 0.6% where it claims 5% — conservative, which is a loss of power rather than an error, and nothing on the output says so. Adjusting puts it back at 5.4%. Both re-randomised versions are at their nominal level by construction, whatever statistic goes into them.

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.

covadapt · Assignment Sixteen candidates nobody would have run, and what they cost. At φ = 0.65 one candidate in the original set is genuinely better than the benchmark, and the question is how often each procedure finds it. The added candidates are stale copies of the last value — read two, four, six … steps late — every one of them worse than the benchmark by at least 43%, and not one of them is ever the best candidate in a sample. The reality check goes from 35.5% to 0.0% as they are added, because its reference distribution has to assume every candidate is exactly as good as the benchmark and sixteen such assumptions is a critical value nothing reaches. The recentred version, which drops from the recentring the candidates the data has already ruled out — 15.1 of 24 of them — goes from 25.5% to 24.5%. The top line never moves: reporting the winner's own p-value cannot notice a change to a set it never looks at.

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.

ranking · Multiplicity Where the +1 matters, and why nobody has noticed that it does. The true size of the two rules at every B, computed rather than simulated: under the null the count of re-randomisations reaching the observed statistic is uniform over {0 … B}, so both sizes are integer arithmetic. With the +1 the size is (⌊α(B+1)⌋)/(B+1), which never exceeds 5%. Without it the size is (⌊αB⌋+1)/(B+1), which is larger except at B = 19, 39, 59 — the values with B + 1 a multiple of 1/α, and the values everybody uses. At B = 19 the two rules are the same rule; at B = 20 the uncorrected one is a 9.5% test. The marks are simulated on 500 trials of 120 patients, as the second route to the same numbers.

The plus one and the round number

A sampled randomisation test counts the observed allocation as one of its own reference draws, and the correction is invisible at B = 19, 39, 59 and 999 — every value anybody uses. At B = 20 the version without it is an 8.00% test where the corrected one is 3.80%, and the convention protecting everybody is a preference for round numbers minus one.

exact · Reference Two constructions on one triangle, and a third that is not. Three resamplings that all keep runs of neighbours, on the same residuals at a block length of 5, with the lags running past ℓ so that the tapers separate. A blocked multiplier never moves a residual; a fixed-length moving block moves every one; and they attenuate identically, worst gap 1.4 standard errors, both sitting on γ_resid(k)(1 − k/ℓ)⁺ and both exactly zero past ℓ — so the attenuation is the block boundary rather than the multiplier. The third is the stationary bootstrap, whose runs are geometric rather than fixed: its taper is γ_resid(k)(1 − 1/ℓ)^k, it agrees with the other two at the first lag and at no other, and at lag 6 it still carries 0.0081 where they carry -0.0005.

The triangle that was not the multiplier's

A resampling that leaves each residual on its own row can keep only what the residuals have, times a triangle. A construction that moves every one of them has the same triangle — and the one in this collection's own table has a different taper entirely.

banded · Bootstrap Each repair is for its own defect, and one is for both. The 95% point of the statistic's own distribution in each world, against the mean 95% point of five reference distributions built from one sample. Where the error variance is a function of the design, the two resamplings that detach a residual from its row fall short and the two multipliers that keep it there do not; where the rows repeat each other it is the other way round. With both defects at once the blocked multiplier — drawn once per run of 5 rows, so the residual never moves and its neighbours share a sign — is the closest of the five, at 2.999 against a truth of 3.803. It is still short by 0.804, and that shortfall is the next figure.

Two defects and one resampling

Four resamplings, each the repair for one defect and wrong about the other. Put both defects in the same world and the statistic's 5% point is 3.8028, where the best of the four reaches 2.8326 — until a multiplier that stays on its own row and shares a sign with its neighbours reaches 2.9988.

proxy · Bootstrap Three analyses of the same trials, none of them wrong about the data. 320 trials at n = 60 with no treatment effect at all, so every rejection counted is a false one, and a covariate that drives the outcome with coefficient 1. The unadjusted comparison is at 5.94% after a coin — its level — and at 0.00% after the rule that reads the covariate: the design removed the imbalance and the analysis is still pricing it. Adjusting for the covariate gives 4.06%, and the rule's own reference distribution — hold the outcomes, re-run the rule 199 times, count — gives 3.13% against the 4.5% that 199 draws can deliver. The last of the three has to be told the assignment rule and nothing else, which is the one thing the experimenter certainly knows.

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.

continuous · Randomisation Welch's test on skewed groups: the low and high rejection rates in every cell, with equal means throughout. Each cell should read 2.5 / 2.5. Two identical exponentials at 20 and 20 read 2.04 / 2.22; the worst cell, a wide exponential against a normal at 8 and 32, reads 9.79 / 0.47.

The skewness of a difference

Welch's test holds its size to within half a point when both groups are normal. Give both groups the same skewed population and it still balances at twenty and twenty — and at eight and thirty-two it rejects low on 7.16% of samples and high on 0.66%. One number decides which: the skewness of the difference of the two means, which ranks twenty-five cells by their imbalance with a correlation of 0.997.

tails · Student What each construction carries, against what there was. The autocorrelation of a resampled error series at five lags, averaged over 60 samples of 40 resamples each. Three facts are in the picture. The residuals lie below the errors at every lag, which is the ceiling a multiplier cannot exceed. The blocked multiplier and the fixed-length block lie on top of each other below it — they attenuate identically, because the attenuation is the join — while the stationary bootstrap, whose runs are geometric rather than fixed, sits above them both. And the sieve is the exception in kind rather than in degree: at lag six it carries 0.0638 where the residuals have 0.0300 and the multiplier has -0.0011, because a fitted model extrapolates past the lags it was told about and a truncated sample sequence cannot.

Errors generated from a fitted model

The one construction that is not bounded by the residuals, because a model extrapolates past the lags it was told about and a truncated sample sequence cannot. It is nearly exact where the only defect is dependence, and it pays for it where there are two.

banded · Reference What a guesser gets, and what a guesser gets for nothing. 600 trials of 150 patients under a fully deterministic rule, with an investigator who knows the rule, the factors and every assignment so far. The guess rate falls with the number of arms — 87.8% at 2, 86.2% at 3, 81.0% at 4 — which reads like a trial getting safer and is not: what a guesser can trade on is the excess over the 50%, 33%, 25% they would get by naming an arm at random, and that goes the other way, from 1.76× chance at two arms to 3.24× at 4. The gap a guesser manufactures between the best and worst arm under a true null is 0.759, 0.733, 0.711 standard deviations — nearly unchanged.

Guessing one arm in three

A balancing rule is guessable because it is balancing. With three arms the next assignment is worked out less often than with two — and by more, relative to what a guesser gets for nothing, and the damage they can do is almost unchanged.

multiarm · Assignment A bias against a variance, with the answer in between. How wrong one sample's reference distribution is, split into the two things it is wrong by. Sharing the multiplier over more rows keeps more of the dependence and closes the bias from 1.688 to 0.835; every row it is shared over also removes an independent sign from the 101 the sample started with, and the spread of the resulting quantile rises from 1.307 to 2.172. The distance a practitioner with one sample is actually exposed to is the two together, and it is smallest at ℓ = 5.

How long a block a multiplier shares

Sharing a sign over more rows keeps more of the dependence and leaves fewer independent signs to build a distribution from. The bias falls from 1.6885 to 0.8479 and the spread rises from 1.3073 to 2.1716, and the rejection rate walks straight through its nominal level on the way from 11.3% to 1.3%.

proxy · Reference What each analysis does at a true null, by shape. Four analyses of the same trials — 500 of them at each shape, 120 units, assigned by the rule that reads the covariate. Every rejection is false. The unadjusted analysis is the one that moves: 1.60% against a linear outcome, where the design removed a great deal that the standard error still prices, and 5.20% against a quadratic, where it removed nothing and the standard error is right. Adjusting holds the level in all three columns, and so does the design's own reference distribution, which needs to be told the rule and nothing else.

The analysis and the shape

An unadjusted analysis after a rule that read the covariate is too cautious — by a third against a linear outcome, by nothing at all against a quadratic. And an adjustment for the wrong function recovers almost none of the precision the right one would.

shape · Randomisation What the corner costs when the table is full of hopeless candidates. The benchmark holds two predictors, one of which is worth 1; a third predictor, worth the amount on the horizontal axis, is held only by candidates the benchmark does not contain. At the left the null is true and both procedures hold their level. To the right there is a genuinely better candidate, and the uncorrected reality check finds it 2.7% of the time while the same test with the clearly bad columns recentred finds it 51.0% of the time. The columns doing the damage are the ones nobody would have looked at twice: they are so far behind that they cannot win, and calibrating as though they might is what makes the test blind.

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.

select · Reference Three estimates of the same effect, and the honest one is the worst. 8,000 trials in which every arm has an effect of exactly 0. The arm carried forward is reported by its first stage at +0.187 above the truth — it was chosen for being ahead — and by its second stage at -0.0032, which is unbiased by construction because the selection could not see it. The combination that gets published is at 0.123, exactly the share of the first stage's bias the first stage contributes. Root mean squared error: 0.240, 0.261, 0.182 — the unbiased estimate is the least accurate of the three.

The estimate after the choice

An arm chosen for being ahead is ahead by more than it should be, and the trial then publishes the average of the stage that chose it and the stage that did not. The unbiased estimate is the one built from a third of the data — and it is the least accurate of the three.

adaptive · Curse Twenty residual plots from data where the model is exactly right, n = 24. Every panel is a correctly specified linear model with normal errors. The apparent curvature, funnelling and outliers are all produced by noise, and the largest single residual across the twenty is 2.13 standard deviations of the error. This is the reference nobody has when judging a real residual plot.

Twenty residual plots

Judging whether a residual plot looks wrong requires knowing what a correct one looks like, and almost nobody has seen twenty of those. Here they are, from a model that is exactly right, at the sample size that matters.

regression · Qq The rate falls geometrically; the count does not fall at all. The share of equal splits of two hundred units that a tolerance of 1 coin-spreads admits, against the number of functions the tolerance is stated for, with the closed form (2Φ(1) − 1)^k drawn beside it. The rate falls by about two thirds with every constraint. The admissible count is that rate times C(200, 100), and it goes from 2^195 to 2^192 — it does not fall in any sense a trial cares about. What the falling rate costs is sampling: 9,878 draws to collect a thousand admissible ones at six constraints, against 1,465 at one.

What a reference distribution costs to sample

A randomisation test on a trial too large to enumerate has to sample its reference distribution, at 1/p attempts per draw and a p-value resolved to 1/(B + 1). Six constraints cost 9,878 attempts per thousand draws, and a thousand draws resolve p to 9.99·10⁻⁴ and not one digit finer.

product · Reference The cheap repair needs a number nobody has. The obvious alternative to re-randomising is to simulate the design under its null once and use the critical value that comes out — which is what the arm-dropping design does, where the critical value has to be solved for and is 2.313. It does not transfer here. The rule chases outcomes, so how imbalanced the allocation gets depends on how often anything succeeds, and the critical value moves from 1.668 at a success rate of 0.05 to 2.718 at 0.8. Calibrated at 0.3 and used at 0.8 the test's real size is 12.4%; used at 0.05 it is 0.12%. The randomisation test needs none of this, because it conditions on the outcomes that happened rather than on a rate they were supposed to come from.

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.

exact · Nuisance Eight encompassing nulls, all of them true at once. The forecast under test is the variance-minimising combination of the eight candidates, and the first-order condition that defines its weights is cov(e_c, e_j) = var(e_c) for every j — so every one of the eight nulls is exactly true simultaneously and every rejection counted here is false. 800 draws of 60 origins. The largest of the eight statistics rejects 25.0% of the time at a nominal 5% and one comparison stated in advance rejects 3.1%, which makes the set worth about 9.1 independent comparisons — nearly the eight it has. Bonferroni, which is far inside its level on a search over accuracy comparisons of the same eight forecasters, is at 4.8% here.

When every null is true

A reality check assumes that every candidate in the set is exactly as good as the benchmark, which is a configuration nobody's data is ever in. Test a combination against its own parts and that configuration is not assumed — it is what the arithmetic makes true.

search · Multiplicity The false discovery rate of twenty correlated tests, against the correlation. BH, every null true: 5.08% at 0, 4.86% at 0.3, 3.70% at 0.6, 2.34% at 0.9. BH, 10 of 20 real: 2.55% at 0, 2.53% at 0.3, 2.26% at 0.6, 1.66% at 0.9. BY, every null true: 1.46% at 0, 1.31% at 0.3, 1.03% at 0.6, 0.69% at 0.9. BY, 10 of 20 real: 0.72% at 0, 0.75% at 0.3, 0.64% at 0.6, 0.50% at 0.9. 20,000 families at each correlation.

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.

multiplicity · Multiplicity How long an honest forecaster looks broken for. The calibration error shown by a forecaster with no miscalibration in it at all, at five record lengths, drawn against one over the square root of the length so that the closed form is a straight line through the origin. It is 0.1252 at fifty forecasts and 0.0090 at ten thousand, against a closed form of √(2K/πn) times the mean root bin variance which gives 0.1257 and 0.0089. The threshold drawn across it is 0.02, a figure routinely read as evidence that something is wrong; the mean falls under it at 1976 forecasts and the 95th percentile at about 4111. Below that, an honest forecaster and a miscalibrated one are being told apart by a statistic that is mostly the sample size.

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.

calibrate · Calibration Twenty runs simulating an exactly 95% interval, checked every 250 replications. Each line is one run's running estimate; the dashed band is where the Wilson interval of the running estimate still contains 95%, and a run stops, marked, the first time it leaves the band. 8 of these twenty stop before 10,000 replications. The exact probability of stopping, from the recursion over the count, is 29.54%.

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.

method · Seeds Forty trials at a true effect of 0.16, under the rule "power at the trend < 10%". The upper line is the benefit boundary (4.56, 3.23, 2.63, 2.28, 2.04); the lower line is where the rule stops a trial for futility (0.40 at 80, 0.66 at 160, 0.95 at 240, 1.31 at 320). Of forty trials with a real effect, 29 cross for benefit and 11 are stopped for futility.

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%.

sequential · Stopping Storey's estimate of the share of true nulls over twenty thousand families, independent and correlated at 0.6. The true share is 0.5. Independent tests: mean 0.610, spread 0.160, below half the truth in 0.92% of families. Correlated at 0.6: mean 0.609, spread 0.240, below half the truth in 9.33%.

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.

multiplicity · Multiplicity An exact test rejecting a true hypothesis a fifth of the time. How often each analysis reports an effect when the average treatment effect is exactly zero and the effect varies between units, at 150 units with 25% treated. The permutation test on the difference in means reads 4.20% where the effect is constant — where the two nulls coincide and its exactness applies — and 22.93% where the effect varies with a standard deviation of 3. The same test on the studentised difference reads 6.27% there, and the ordinary large-sample t, which makes no exactness claim at all, reads 6.60%.

The null the exactness is for

A permutation test is exact under the hypothesis that the treatment changed nothing for anybody. Under the hypothesis it changed nothing on average, with a quarter of the units treated and the effect varying between them, it rejects a true null 22.93% of the time.

exact · Nuisance The bounded error and the unbounded one. How the sequential trace procedure's answer is distributed, against the sample length, for a three-series system with 2 genuine relations. Over-counting — claiming a stationary combination that is a random walk — reads 4.9%, 7.2%, 5.7%, 6.2%, 5.9%, 4.2% across the six lengths, never far from the 5% of a single test. Under-counting reads 69.5%, 40.2%, 14.0%, 0.5%, 0.0%, 0.0%. The procedure is described as a 5% rule and the 5% applies to one of those columns.

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.

systems · Rank The chance of crossing later from each interim z, under six schedules with O'Brien–Fleming-type spending boundaries. Exact. At an interim |z| of 1.0: end only 3.64%, +0.6 3.41%, +0.75 3.20%, +0.9 3.41%, every 0.125 3.00%, every 0.05 2.88%. At 2.5: end only 38.30%, +0.6 45.80%, +0.75 45.36%, +0.9 41.70%, every 0.125 50.08%, every 0.05 53.24%. The heavy line is the largest of the six at each z.

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%.

sequential · Stopping Twenty hypotheses tested in a declared order, the ten real effects listed first. Effects of three standard errors, ten real, familywise 5%. fixed sequence: 85.3% at position 1, 45.0% at 5, 20.4% at 10; overall power 46.10%; fallback: 49.1% at position 1, 56.4% at 5, 57.9% at 10; overall power 55.87%; Holm: 52.5% at position 1, 52.2% at 5, 52.5% at 10; overall power 52.53%.

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.

multiplicity · Multiplicity

Named alongside it

The objects these essays reach for when they reach for this one.

Monte CarloReference distributionStatistical powerNull hypothesisCritical valuep-valueRandomisation testAdaptive designBlock bootstrapMultiple comparisonsBenchmark forecastExperimental design

All concepts