Balancing towards unequal targets

The allocation field’s whole subject is that equal allocation is a default rather than an optimum. A shared control against k treatments should be sampled √k times as heavily as each treatment; an arm with more variance should be sampled more; an arm that costs more should be sampled less. Every one of those rules produces a target ratio that is not one to one.

The covariate-adaptive field’s whole subject is a rule that keeps the arms comparable on what was recorded before treatment. Its score, at every arrival, asks which arm makes the counts inside the patient’s factor levels most even.

Put the two together and the second quietly destroys the first.

What a raw-count score delivers #

Take a three-arm trial designed to allocate 2:1:1 — a control arm at half the patients and two treatments at a quarter each, which is what one control against several treatments calls for. Run minimisation on the counts as they stand.

The weighted score delivers 49.9 : 25.1 : 25.1. The raw-count score delivers 33.4 : 33.3 : 33.3.

It is not approximately wrong. The design has been replaced, arm by arm, with an equal-allocation trial, and every quantity that depended on the ratio — the power of the control-versus-treatment comparisons, the precision of the control mean, whatever cost calculation produced the 2:1:1 in the first place — has been silently recomputed at the wrong numbers.

Why it happens, which is not a bug #

Nothing has gone wrong inside the rule. Minimisation was asked to make counts even and it made them even; evenness inside a factor level is exactly what a raw-count score measures, and a 2:1:1 trial is maximally uneven by that measure. The rule spends every arrival correcting the imbalance the design asked for.

The randomisation step does not save it either. Minimisation is usually run with a probability p of following its own preference — 0.85 here — and the remaining probability spread over the other arms. That randomisation is symmetric across arms, so it pulls towards equality as well.

The repair is to compare each arm’s count against its target rather than against the other arms: divide by the share that arm is meant to receive, and then measure the spread of what comes out. An arm at half the patients and an arm at a quarter of them are perfectly balanced in that scale when they hold exactly twice and once of something, which is what the design meant by balanced all along.

That is one division, it costs nothing, and it turns 33.4 : 33.3 : 33.3 into 49.9 : 25.1 : 25.1.

How the failure grows with the ratio #

The worst departures are 0.0 points at 1:1:1, 16.6 at 2:1:1, 26.5 at 3:1:1 and 33.1 at 4:1:1. That is the shape it has to have: an unweighted score always delivers equal allocation, so the error is exactly the distance between the design and equality, and it grows without limit as the design becomes more unequal.

Two consequences follow and both are worth stating in the form a trialist would meet them.

The failure is invisible in a 1:1:1 trial, where the two rules agree exactly, so a procedure validated on an equal-allocation trial and reused on an unequal one carries no warning.

The failure is largest exactly where the ratio was most deliberate. A 4:1:1 design is not an accident; somebody computed it. It is the design whose intention is most completely undone.

The three scores, under an unequal target #

The previous essay’s three ways of measuring unevenness all need the same repair and none of them supplies it. The range of standardised counts, their variance and their pairwise sum are three summaries of the same standardised vector, so the weighting sits underneath all three and the choice between them is unchanged by it.

That is worth one sentence rather than a section, and the sentence is that the two choices are independent: which score, and what it is measured on. A trial report that says “minimisation” has left both of them unstated, and the second is the one that can move half the patients.

What it costs, in the currency the design was chosen in #

The allocation field measures why unequal ratios exist, and each of its reasons converts the departure above into a loss.

A shared control. With k treatments against one control, the variance-minimising allocation puts √k times as many units on the control as on each treatment. At k = 2 that is 1.41 : 1 : 1, at k = 4 it is 2 : 1 : 1 : 1 : 1. A rule that equalises the arms is running the design that field measures as suboptimal, and the loss it computes there is the loss here.

Unequal variances. The optimal allocation is proportional to the standard deviations, and the same argument applies unchanged.

Cost. The optimal ratio is proportional to σ/√c, and an equalised trial simply spends more money for the same precision.

In every case the arithmetic of what is lost is in the allocation field, and what this essay adds is that the loss can be incurred by a rule that was never asked about ratios at all.

That last picture is the one worth keeping. A larger trial does not fix this, because the rule is converging on the allocation it was told to produce; it was told the wrong one.

How much of the repair the randomisation step manages on its own #

The section below says randomising in the target proportions is “nowhere near sufficient”, and the four departures already measured say exactly how near.

If the raw-count rule delivered perfect equality the departure would be the whole distance from the design to equality: 16.7, 26.7 and 33.4 points at 2:1:1, 3:1:1 and 4:1:1. The measured departures are 16.6, 26.5 and 33.1.

So the 1 − p branch — fifteen per cent of arrivals, spread in the target proportions — recovers 0.1, 0.2 and 0.3 points of the correction needed. As a share of the damage that is 0.6%, 0.8% and 0.9%.

A repair that delivers under one per cent of what is required is not a partial repair. It is a repair that leaves the number in the report indistinguishable from no repair at all, and it grows in absolute terms with the ratio, which is exactly the pattern that makes it look like it is doing something.

Which quantity the equalisation actually damages #

“Every quantity that depended on the ratio has been recomputed at the wrong numbers” is true and it is worth saying which ones move and by how much, because they do not all move and one of them moves the other way.

Take a hundred and eighty patients and the variance of a single control-versus-treatment difference, which is proportional to $1/n_c + 1/n_t$.

• At 2:1:1 the arms hold 90, 45 and 45, giving 1/90 + 1/45 = 1/30. Equalised at 60, 60, 60 it is 2/60 = 1/30. Identical, exactly.
• At 4:1:1 the arms hold 120, 30 and 30, giving 1/120 + 1/30 = 1/24. Equalised it is 1/30, which is 20% better.
• At the √k optimum for two treatments, 1.41:1:1, the arms hold 74.5, 52.7 and 52.7, and the sum is 2.9% below either of the above.

So on a single pairwise comparison, equalising a 2:1:1 trial costs nothing at all and equalising a 4:1:1 trial is an improvement. The √k rule is what the shared-control argument produces for two treatments, and it is 1.41 rather than 2 — so neither 3:1:1 nor 4:1:1 comes from that argument in the first place.

What the equalisation does destroy is the control mean itself. At 2:1:1 the control’s variance goes from σ²/90 to σ²/60, half as large again; at 4:1:1 from σ²/120 to σ²/60, twice. A design that puts two thirds of its patients on the control is a design estimating the control precisely — because it is a reference for several comparisons at once, or because a cost or variance argument put it there — and that is the quantity the raw-count rule halves the precision of.

So the loss is real and it is not where the ratio’s usual justification points. A trialist checking whether the equalisation mattered by recomputing one pairwise power will find nothing wrong, which is the worst possible outcome for a defect this large.

Where the weighting has to go, exactly #

The repair is one division and it has to be in the right place, which is worth spelling out because there are two plausible places and only one of them works.

Inside the score, before the spread is measured. Each arm’s count is divided by its target share and the imbalance is measured on the standardised counts, so an arm holding twice as many patients as another is balanced when its target is twice as large.

Not in the randomisation step alone. Giving the preferred arm probability p and spreading the rest in proportion to the targets — which this implementation also does — is necessary and nowhere near sufficient: with an unweighted score, the preferred arm is whichever arm is behind on raw counts, so the rule spends its p pulling towards equality and its 1 − p pulling towards the target. The result is a compromise nobody designed, and at 2:1:1 with p = 0.85 it is much nearer equality than the target.

The distinction matters because the second repair is the one that looks sufficient. An implementation that randomises in the target proportions and scores on raw counts will produce arm sizes that are wrong in a way that varies with p — which is a parameter chosen for predictability reasons — and nothing in the output will connect the two.

The coin costs the ratio a little even with the score weighted, and the cost grows with how unequal the design is. At 4:1:1 the weighted rule delivers 67.0% of the runs to the first arm at p = 1, 66.0% at p = 0.85 and 62.3% at p = 0.7, because the 1 − p branch spreads over the other arms in proportion and cannot pull as hard as the score does. At 2:1:1 the same sweep runs 50.2%, 49.9%, 49.1%. It is a second-order effect beside the sixteen and thirty-three points a raw-count score gives away, and it is the reason the check on this figure is a relative bound rather than an absolute one.

A design decision is not a preference #

One more framing, because it is the reason this essay sits in the allocation field’s ladder rather than the assignment field’s.

The allocation field’s rules are derived: √k for a shared control, proportional to σ for unequal variances, proportional to σ/√c when the arms cost different amounts. Each is the solution of a minimisation with a stated objective, and the ratio it returns is not a taste. It is the answer.

A balancing rule that overwrites it is not making a trade-off between balance and allocation — it is not aware there is anything to trade. The weighted score is what turns the two into a genuine joint problem, at which point they compose without conflict: the ratio decides how many, the score decides which, and neither has to give anything up.

The alternative that does not need the repair #

There is one rule in the covariate-adaptive family that handles unequal targets without any weighting, and it is worth naming because it is what many trials use.

Permuted blocks hold the ratio by construction: a block of four containing two controls and one of each treatment delivers 2:1:1 exactly at the end of every block, whatever the covariates do. What blocks do not do is balance any covariate — the two-arm field measures a stratified block scheme failing exactly where the cells are thin, and blocks without strata balance nothing at all.

So the choice is between a rule that gets the ratio right and the covariates wrong, and a rule that gets both right provided somebody remembered to divide by the target. That is not much of a choice, and the reason it is worth an essay is that the second rule fails silently: a blocked trial that loses covariate balance shows it in the baseline table, and a minimised trial that loses the ratio shows it only in the arm sizes, which are usually reported as the number of patients recruited rather than as a design decision that was or was not honoured.

What the weighted score does to balance #

A fair question about the repair is whether it costs anything in the balance it was there to buy. It does not.

At 2:1:1 the weighted rule leaves a worst standardised margin of 3.17 against the raw-count rule’s 21.72 — the raw-count rule is worse on the very quantity it was optimising, once that quantity is measured on the scale the design defined. That is not a coincidence: the standardised margin asks how far each arm is from its own target, and a rule driving all three arms to a third is driving two of them a long way from theirs.

Measured on its own scale the raw-count rule wins, and measured on the design’s scale it loses badly, which is the same lesson the previous essay’s three scores taught in a milder form. A comparison between allocation rules has to state what balance means before any of it means anything.

Why nobody notices #

The failure has three properties that between them make it hard to see, and they are worth listing because they are the properties that make any silent defect survive.

It produces a perfectly ordinary trial. Equal allocation is not a pathology. The arms are balanced on the covariates, the analysis runs, the standard errors are honest for the trial that was run, and every diagnostic a trialist looks at is clean.

The number that is wrong is one nobody treats as an output. Arm sizes are reported as a fact about recruitment, not as a design parameter that was met or missed, so the comparison against the target is a comparison nobody makes.

The loss is in power rather than in validity. Nothing here inflates a false-positive rate or biases an estimate; the trial is simply less efficient than the one that was designed, and a trial that misses significance for that reason looks exactly like a trial whose effect was smaller than hoped.

This is the same shape as the two-arm field’s finding that an unadjusted analysis after minimisation is conservative rather than anticonservative: a defect that costs power and breaks no rule is a defect that nothing in the standard apparatus is looking for.

What is claimed, and what is not #

The claim is what an unequal allocation ratio does to a covariate-adaptive rule, and what the rule does to it: the delivered shares under both scores, the departure as a function of the ratio, its invariance to the size of the trial, and the standardised margin under each.

What stays out: response-adaptive ratios that change during the trial, which belong to the adaptive field and where the target is a moving object; allocation ratios chosen to maximise power against a specific alternative rather than to minimise a variance; and the analysis of an unequally allocated trial, where the unequal arms change the degrees of freedom and the multiple-comparison structure — that is Dunnett’s problem and it is measured there.

What to check in a report #

Three things, all of which a reader can do from the arm sizes alone, and none of which requires the allocation code.

Compare the realised shares against the design. A 2:1:1 trial that recruited 180 patients should report about 90, 45 and 45. A report of 60, 60, 60 under the heading of minimisation is this failure, and it is not a recruitment accident — the arms are too equal, not too unequal.

Look at how the imbalance was defined. If a protocol says the rule minimised the difference in the numbers allocated within each stratum, the score is on raw counts and the ratio was not protected.

Check whether the ratio was ever tested. An implementation validated on an equal-allocation trial has never exercised the code path that matters here, because at 1:1:1 the two scores are the same function.

The checks, and the refusal #

Two claims are gated and one refusal carries the field. The weighted score must deliver every arm’s target share to within two points, and the raw-count score must miss the first arm’s by more than five — which is the repair and the failure asserted as bounds rather than described. The departure must grow with how unequal the target is, at every ratio measured.

The refusal is the raw-count score itself, against the standard that a rule asked for 2:1:1 delivers 2:1:1. It delivers 33.4 : 33.3 : 33.3, off by 16.6 points, where the weighted score is off by 0.1. The check requires it to fail, because an assertion that has never rejected anything proves nothing.