Every essay — page 9
Splitting the units
The only design decision that costs nothing: the same units, the same measurements, the same analysis, and a different variance. Sample the noisier arm more, the expensive one less, and the shared control by the square root of the number of arms — and then notice that every one of those rules is a function of a quantity nobody has, and measure what happens when it is estimated instead.
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 cost of a unit
Change the constraint from units to money and the allocation rule changes with it — from σᵢ to σᵢ/√cᵢ, which can point the other way. An arm that is noisy and expensive gets fewer units than the same arm would if the money were not the thing running out.
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.
Allocating on a guess
Every allocation rule in this field is a function of quantities the experiment is being run to find out. Fed a pilot's estimate of them, the rule that minimises the variance makes the experiment worse than not bothering — until the arms differ by about a factor of two, which is further than anyone would guess.
The arm whose variance is its answer
With a binary outcome the allocation rule is a function of the proportions the trial exists to estimate. It costs at most 4.36% of variance to ignore it anywhere between a tenth and nine tenths, because √(p(1−p)) stays within a factor of two of its peak across 98% of the unit interval.
Two contrasts, one split
A risk difference wants 62.0% of the units in the first arm, a log risk ratio wants 21.4% and a log odds ratio wants 38.0% — on one dataset, with one pair of proportions. The difference's rule and the odds ratio's are exact reflections of each other, so no split can be near-optimal for both.
A contrast chosen after the data
A two-arm trial with a binary outcome that reports whichever of the risk difference, the log risk ratio and the log odds ratio comes out most significant has tested three statistics that ask one question. At an equal split the choice is no choice at all: the difference has the largest z in every one of twenty thousand trials, so the selected test is the difference's, at its 5%. At a 30–70 split the choice is real and costs a point and a half of false positives, 6.5% at the rarest outcome. Pre-registering the difference and the odds ratio as a pair with Bonferroni's correction — the cautious alternative — costs eight to twelve points of power at every split.
Designs that change while they run
The stopping-rule field is a fixed design looked at more than once. Here the design itself is a function of the data — how many units, which arm the next one goes to, which arms survive the interim — and the question stops being what the rule spends and becomes what it leaves behind. The estimate from an arm chosen for being ahead is ahead by more than it should be, and the unbiased estimate is the one that throws away the data the choice was made on.
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.
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.
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.
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.
Shrinking the arm that was chosen
A trial that carries the best of eight arms forward reports it as better than it is — by +0.123 when the eight arms are alike — and its second stage alone is unbiased but the least accurate of the estimates. Pulling the chosen arm's first stage back towards the eight arms' mean before combining removes most of the bias when the arms are alike (+0.020) and gives the smallest error of any estimate, 0.133 against the published 0.182. When one arm really is ahead by half a standard deviation, the same shrinkage pulls the true winner back towards the losers and understates it by 0.103, with more error than the published estimate. The weight is estimated from eight numbers, and it is right when the selection was noise and wrong when the selection was right.
A prior that lets one arm stand out
Shrinking the chosen arm of eight under a normal prior understates a genuine winner by 0.103. A t prior on three degrees of freedom with the same spread understates it by 0.101 — the tail is too far out to reach a lead of three and a half standard errors. A prior with a fifth of its weight on a vague component understates it by 0.073, costs 0.010 of bias when the arms are alike, and still has more error than the unshrunk estimate. With sixteen arms the same mixture recovers three fifths of the loss, because a bell of fifteen shows its outlier; with eight, the arms put more than half their posterior weight on 'one stands out' in 0.4% of trials where one does.
A second stage sized by the first
A drop-the-losers trial can size its second stage by what the first stage says about the arms' shape — more patients when the chosen arm's lead looks like luck, fewer when it looks real. The rule does what it was built to do: at sixteen arms with a genuine winner it spends 51.0 patients a group when the interim chose the wrong arm and 24.2 when it chose the right one. And it buys nothing. Against a fixed second stage of the same average size, every estimate of the chosen arm errs by the same to within a few thousandths; the published combination's bias rises from 0.014 to 0.022, and the second stage alone, still unbiased, errs by 0.319 against 0.281.
Patients spent before the choice
A trial that picks the best of eight arms and then confirms it splits its patients between choosing and estimating, and the familiar shape — sixty an arm before the choice, thirty after — spends ninety per cent of a six-hundred-patient budget on the choice. Measured against the effect a reader is told about, the best arm's, that split is nearly right when one arm is modestly ahead and twice as wrong as it needs to be when the arms are alike. A split of thirty-two an arm before the choice is never more than 21.3% worse than the best split for whichever world holds; sixty an arm can be 98.8% worse. The two targets an estimate could serve — the chosen arm's effect and the best arm's — pull the split in opposite directions, and only one of them is what gets published.
The reference distribution the design supplies
Hold the outcomes fixed, re-run the rule that assigned them, and count. A p-value built that way needs no assumption about the outcomes, no large-sample argument and no nuisance parameter — it needs to be told the rule, which is the one thing the experimenter already knows. It repairs the adaptive design the previous field leaves broken, and it is not free.
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%.
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%.
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.
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.
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.
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 repair, with a covariate in it
Studentising a permutation test's statistic made the difference in means exact under the sharp null and nearly right under the weak one. Carried to the covariate-adjusted estimate a trial actually reports, the repair works only if the adjustment includes the treatment-by-covariate interaction. With a quarter of 150 units treated and effects that vary with the outcome, the adjusted estimate's permutation test rejects 14.8% of true weak nulls; over its sandwich standard error, 3.0%; the interacted estimate over its sandwich, 3.9%. When the effect varies with the covariate itself, even an even split does not protect: the adjusted test rejects none of a thousand true weak nulls, and at an average effect of 0.2 its power is 5.2% against the interacted, studentised test's 40.7%.
The covariate chosen afterwards
A trial that chooses which baseline covariate to adjust for after randomisation has two ways to run its permutation test: hold the chosen covariate fixed across the shuffles, which is what an analysis that reports adjusting for it actually does, or re-make the choice inside every shuffle, which is exact by construction. Holding it fixed, a choice made on significance rejects 10.4% of true sharp nulls, a choice made on imbalance only 3.0% — and pays seven and a half points of power for it — while a choice that never reads the arm labels is the same test either way. The interacted, studentised statistic keeps its weak-null behaviour only when the covariate chosen is the one the effect varies with.
Coverage without a distribution
Every interval counted here so far has been found short of what it promised. This one is not, and the reason is that it is not a statement about the data at all: the rank of a future observation among a set of exchangeable calibration scores is uniform, so an interval built at the right order statistic covers a stated share of the time at any sample size, under any distribution, around any model however wrong. What it does not say is where that coverage sits — and everything the procedure does not know turns up in the answer to that rather than in the total.
