Every essay — page 5
The value that is not there
A missing value is missing conditional on something, and which something decides everything that follows. Dropping the incomplete rows leaves a regression slope exactly right when the chance of being observed depends on the regressor, however strongly, and wrong by a quarter of itself when it depends on the outcome — and the data cannot tell those two cases apart. Filling the gaps in is not free either: one filled value is not an observation, and the arithmetic that makes several of them into one is two corrections rather than the one everybody quotes.
Three mechanisms and one dataset
Four rules for which outcomes go missing, each calibrated to lose the same 35% of the rows and each leaning on what it reads with the same coefficient. Three leave the fitted slope exactly where it was, and the one that reads the outcome moves it by 0.163531.
Dropping the incomplete rows
Push the missingness until the rows that survive have a covariate mean of 0.543905 against a population zero and a variance of 0.5041 against one, and the fitted slope is still exactly right. Where the rule reads the outcome instead, the same sweep takes coverage to 2.42% at eight hundred rows.
One imputation is not an observation
Three ways of filling a missing outcome, under a mechanism that makes dropping the rows beyond reproach. Filling with the observed mean covers 13.85%, filling with a fitted value covers 80.85%, adding noise covers 85.78%, and the thing all three were meant to improve on covers 95.93%.
The variance between imputations
Pooling several filled datasets covers 94.10% at two imputations and reaches its promise at five, where a single fill covered 85.78%. The correction everybody quotes is the smaller of the two doing the work — 1.00 ± 0.22 points against 1.55 ± 0.28.
An imputation model the analysis does not contain
A model that fills the gaps without a covariate the analysis fits attenuates that covariate's coefficient by exactly the missing share, 0.4 to 0.26, and moves the one it did carry by exactly γρf, 0.6 to 0.642. The reverse case is supposed to inflate the interval, and at four strengths of the extra knowledge it does not.
The mechanism the data cannot see
Two worlds produce identical covariates, identical patterns of what is recorded and identical recorded outcomes, to the last bit. Their true slopes are 0.6 and 0.315452, and the truth moves at 0.284548 per unit of an assumption nothing in the data can inform.
The assumption that identifies the mechanism
A selection model estimates how strongly an outcome decides whether it is recorded — the quantity two identical datasets showed no statistic can see — and it does so by assuming the outcome is normal. Where that holds and the outcome does decide, it repairs a slope complete cases put at 0.4318 to 0.5795. Where the missingness is at random and the residual is merely skewed, it reports selection that is not there, moves the slope from 0.5971 to 1.0319, and rejects missingness at random in 72.5% of studies.
A variable that moves recording
A selection model fitted to a skewed outcome that is missing at random reports selection that is not there on three studies in four. Give it a variable that shifts who is recorded and has no place in the outcome — strong enough to carry 29% of the recording index's variance — and the false reports fall to 7.5%, the slope from 1.034 to 0.613 against a truth of 0.6. Leave the same variable out of the model and it does harm instead: false reports reach 100%, and where the outcome really does decide recording, the estimated pull falls from 1.18 to 0.78.
Stopping rules
A p-value is defined relative to a sampling plan, so two experiments with identical data and different stopping rules have different p-values. That sounds philosophical and it is arithmetical: testing five times at the nominal level rejects a true null 14% of the time.
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.
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.
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 outcomes a trial could have stopped with
A trial that stops at its second look with z = 3.3 has a two-sided p-value of 0.000969, 0.000987, 0.00187 or 0.0421, depending on how the outcomes it could have stopped with are ordered. One of the four orderings does not change when the looks the trial never reached are replanned, and the same one gives a trial that ran to the end with z = 6 a p-value of 0.0256.
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%.
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%.
A look added by a rule
A monitoring committee's rule — add a look at three quarters of the trial when the interim |z| is at least 1.5 — spends 5.2323% under O'Brien–Fleming-type boundaries. Written into the protocol it can be given boundaries that spend exactly 5%, three ways: raise the added look's boundaries by 2.05%, raise every later boundary by 0.99%, or preserve at each interim value the chance of crossing the plan would have given. All three cost the same, 0.38 points of power, from 88.94% to 88.56%, because the power the uncorrected rule seemed to keep was the excess error. Made exact, the rule is a design between the two fixed schedules — and at every trigger slightly better than randomising between them.
The variance that contains the effect
A monitoring committee that adds an interim look because the variance came in higher than planned is reading a nuisance quantity, and a look added on a nuisance quantity should leave the spending function's 5% alone. It does, exactly, when the variance is the within-arm one, and when the trigger is the calendar. It does not when the variance is the one computed with the arm labels hidden: that variance is the within-arm sum of squares plus the interim statistic squared, so it is high more often when the trend is strong. The excess is 0.069 points at a twenty-patient interim and falls as one over the square root of the interim's size — a tenth of what a trigger on the trend itself spends, and never zero.
Groups that borrow
Eight hospitals are neither one hospital nor eight unrelated problems, and the estimate between those two answers is not a compromise. It is a weighted average whose weight — se²/(se² + τ²) — is decided by how well each group is measured and by nothing else, and the population spread in it is estimated from the data rather than assumed.
Eight groups, one population
Eight hospitals are neither one hospital nor eight unrelated problems. The two obvious answers cost 2.23 and 1.15 in squared error; the estimate between them costs 0.88, and the weight it uses is not a matter of taste.
The weight that decides
B = se²/(se² + τ²) is not a compromise between two answers. It is exactly the posterior mean's weight, it agrees with a numerical integration to ten digits, and an argument that mentions no population at all arrives at almost the same estimator.
The prior the data estimates
A hierarchical model needs a population spread, and it does not ask for one. It reads τ off the distance between the group means — biased six per cent low, exactly zero on 53% of datasets where the groups are identical — and the prior stops being a belief.
When borrowing goes wrong
Partial pooling wins on the total and can lose badly on one group. Placed six population widths out, the group that was never from the population is estimated six times worse than by its own mean — and nothing in the output says so.
The fewest groups that can borrow
At three groups the estimator that shrinks towards its own data's mean returns the group means untouched, on every dataset, because its constant is J − 3. At two it expands instead of shrinking. And the number of groups at which partial pooling starts to be worth doing is five, or two, or never — it depends on how far apart the groups are.
Where the borrowing goes
Pooling cuts the total squared error across eight groups by 56%. Two of the eight take 61% of that reduction, the four best-measured groups share 11% between them, and the largest group gets 1.5% of what the smallest does. The headline is a fact about the groups nobody was asking about.
One population, or two
Group effects from two clusters rather than one bell, with the same total spread. The analysis recovers the same population spread, uses the same weight for every group, and reports nothing unusual — while 46% of its estimates land in a region holding 6.6% of the truths.
The shape the estimates keep
Partial pooling was suspected of destroying the evidence of its own misfit: compressing a two-cluster population of group effects towards one centre before any test could see the clusters. With groups of equal size it destroys nothing, because every estimate moves the same fraction of the way to the same place and the estimates keep the means' shape exactly — except when the fit pools completely, as it does on 29.9% of eight-group datasets at a spread of one. The evidence was never there: a shape check has 6.5% power at eight groups. With groups of unequal size the pooled estimates see the clusters better than the raw means do.