Theme

The thread: Two routes to a number

Every simulation here has a closed form beside it and every closed form has a simulation. A distribution function and its quantile must invert each other to ten digits; an exact coverage sum and a Monte Carlo count must agree. Neither route can confirm itself, and they share no arithmetic.

Choosing what the rule reads

A basis is a subspace

A balancing rule cannot tell one basis from another with the same span, so choosing what to hand it is choosing a subspace — and then what it removes of any outcome shape is a projection, computable exactly, with no trial anywhere in it.

One experiment, with the blocks getting smaller as the target comes into range. A single run at a requirement of 0.25, with the block sizes 5, 5, 11, 25, 11, 8, 3, 2 and a total of 70 observations in 8 blocks. The rule stops when the observations in hand reach z²σ̂²/d², with σ̂² pooled from the within-block contrasts — an estimate that moves as the run goes on, so the target moves too. Early blocks are large because the target is far away and cannot be overshot; late ones are small because a block is the granularity of the answer. The interval afterwards is built from the 8 block means and from nothing the rule looked at, and it has 7 degrees of freedom against the rule's 62.

The block size as a schedule

A block size that changes

The blinded rule's exactness never needed the blocks to be the same size. Letting the size be chosen from the contrasts as the run goes on leaves the coverage exactly where it was — and runs straight into an identity that says what a schedule can and cannot buy.

Four blocks, and only the ends matter. The weights a block carries, normalised so that the resample keeps the residuals' variance and only their covariances are attenuated. What separates these shapes, for everything that follows, is the value at the two ends and nothing about the middle: the first-order attenuation is −(w(0)² + w(1)²)/(2∫w²), which is -1.0000 for the rectangle, -0.3896 for the trapezoid cut off at half height, and exactly zero for both windows that reach the axis. The half-height trapezoid is in the table to be the case that separates a shape from a boundary value: it is smooth, it is tapered, and it buys none of the order the other two buy.

A block, weighted inside itself

A block weighted inside itself

The triangle every block resample attenuates by is not a fact about blocks. It is the self-convolution of a rectangle, and a block weighted down towards its own ends has a different one — whose leading term is the squared value at the two ends and nothing else about the shape.

The price of each thing the rule is not told. What each rule gives up against the best model available, at a persistence of 0.85 on a fifteen-candidate table, over 400 draws. Reading down: least squares with the ordinary penalty; the whitening at the true ρ; the same at a ρ̂ estimated per candidate; that rule with the term the Gaussian likelihood carries and it omits; a Bartlett-tapered Ω̂ estimated once from the fullest candidate at L = 8; the same estimated per candidate; and the truncated Ω̂, which exists on only 45.0% of draws and is averaged over those. Knowing ρ recovers 89.9% of what counting rows gives up, estimating it 83.4%, and estimating a whole covariance 75.6%.

Estimating the dependence, not naming it

A covariance with no parameter in it

The whitening that repairs a criterion is told the dependence is a first-order autoregression and left to find one number. A real dependence is not one number, and the obvious estimate of it is not a covariance matrix.

What a median split can see. A standard normal covariate with its median marked, and the mean of each category as a vertical rule: -0.7979, 0.7979. A rule that balances the categories is balancing those numbers and nothing else, so the part of the covariate it can act on is the variance between them — 0.6366 of the total, which at two categories is exactly 2/π because the two half-normal means are ±√(2/π). The rest, 0.3634, is variation inside the categories that the rule cannot see and does not touch: the assignment within a category is still a coin. Everything the next figure measures is a consequence of this one, and it is available before any unit has arrived.

Balancing what has no levels

A covariate with no levels

Every balancing rule on this site reads a level. Age and blood pressure have none, so somebody cuts them into categories — and a median split can see exactly 2/π of a normal covariate, whatever the rule does with the halves.

What each rule gives up against an oracle that is arithmetic. Expected squared error of the candidate each rule selects, minus the expected squared error of the best candidate in the table, over 500 draws of 120 rows. Both quantities are closed forms — σ_S²(1 + q/(n − q − 1)) — so the only Monte Carlo here is over which candidate got picked. The hold-out spends half its rows measuring what the criterion computes, and pays 1.8 times as much for it. Schwarz's criterion is worst because it is answering a different question: which candidate contains the truth, rather than which one forecasts best.

Scoring a search without spending data

A criterion is a prediction of the hold-out

A rolling hold-out spends half the sample measuring what a criterion computes from all of it. Against an oracle that is arithmetic rather than an estimate, the criterion gives up 0.01701 and the hold-out 0.03200 — and the number the hold-out reports for its own winner is optimistic by more than either.

The expansion that never terminates. The Hermite coefficients of a median split, in magnitude, against the reference j to the power −3/4, anchored at the first one. Every even order is exactly zero because sign is an odd function, and every odd order is not, so no truncation is exact — where a polynomial of degree d is exact at any order past d. Summed, the tail past J falls like 1/√J: sixty orders still leave 6.6% of the variance outside. That statement is what made a cut dictionary's geometry unavailable in closed form, and it is a statement about the function against itself. What it is not is the accuracy of an inner product between two correlated variables, where every term past J carries a factor of ρ^m as well.

A cut point, at a correlation

A cut is not a polynomial, and it does not have to be

A threshold's expansion never terminates, which is why a balancing dictionary's geometry was closed for powers and taken to draws for cut points. Conditioning on the second variable closes it for both.

Fitted together, or fitted after

A dependence fitted with the line

Every whitening in this collection reads the dependence off a set of residuals, and residuals are not errors. Fitting the two together recovers most of what that costs, and changes almost nothing about the decision it feeds.

Four dependences a single parameter cannot tell apart. Every law here is standardised to a lag-one autocorrelation of 0.8, so a rule told the errors are a first-order autoregression finds the same number in all four and has no way of seeing what separates them. The geometric decay is the world in which estimating a covariance rather than naming it was priced, and found to cost. The five-period moving average has 0.200 at the fourth lag and exactly nothing past it, where the geometric law says 0.328 at the fifth. Long memory at d = 4/9 is still at 0.576 by the twentieth lag, where the geometric law has reached 0.012. The break has no autocorrelation function at all: what is drawn for it is the average over the pairs at each gap, which is what a stationary estimate converges to.

The shape a dependence has

A dependence with a shape

Four ways for errors to repeat, all with the same first lag and nothing else in common. A rule told the errors are a first-order autoregression finds the same number in all four, and is right about one of them.

A design chosen rather than looked up

A design is a number

A standard design is taken from a catalogue and then measured. Turn the arithmetic round and a design becomes the answer to an optimisation — and over 121 candidate settings the search keeps nine of them, which are exactly the nine a catalogue would have offered, at weights nine equal runs cannot express.

Two covariates make the dictionary an outer product. Four functions of each covariate, and everything a balancing rule may be handed. The margins are the 8 main effects and the block between them is the 16 interactions, which are 66.7% of the dictionary. Every inner product in it is closed form — ⟨f₁g₁, f₂g₂⟩ = ⟨f₁,f₂⟩⟨g₁,g₂⟩ when the covariates are independent — so nothing about the geometry gets harder. What gets harder is the counting: choosing k of 24 is C(24, k), which is 10,626 at four and 735,471 at eight.

When the set is too large to walk

A dictionary that is a product

Two covariates make what a balancing rule may read an outer product — eight main effects and sixteen interactions — and every inner product in it is still closed form. What a rule holding all eight main effects removes of a pure interaction is not small. It is zero.

The rule is parity, and it runs both ways. At a correlation of 0.5, four combinations of a dictionary and an outcome shape. The joint sign flip (X, Y) → (−X, −Y) leaves the bivariate normal alone at every correlation, so a function that changes sign under it is orthogonal to one that does not. A product of two odd functions is even; a product of an odd and an even one is odd. So an odd dictionary removes exactly none of the first and something of the second, and an even dictionary does the reverse — which it does, to machine precision, in both of the two rows that should be zero. This is one rule where there had been two: that a median split's square is constant, and that a polynomial dictionary contains the products a correlation generates.

What a dictionary buys and what it costs

A dictionary that is neither

A rule handed two median splits removes none of their interaction; a rule handed two covariates removes none of their product. Those were two results with two explanations, and they are one result with one — and finding it corrected the number underneath both.

A covariance with no parameter

A family before a fit

A regression's coefficients and one correlation can be maximised together. Replace the correlation with an estimated covariance and there is nothing left for "jointly" to mean — until a set of covariances is named, and the set turns out not to contain the truth.

One margin rises; the other turns over. The two halves of the table's margin across the sweep: a lower-tail copula's own leak with a symmetric covariate, and a covariate skewed at 0.95 under a Gaussian copula. The marginal's leak rises at every step, from 3.727% to 36.056%. The copula's does not: it rises to 9.064% at a Spearman of 0.6 and falls to 8.219% by 0.7. It has to turn over, because at a rank correlation of one the two variables are a deterministic function of each other and there is no interaction left for a split to leak. So the margin of the table turns over before any cell in it does.

The same table at seven correlations

A margin that turns over

A skewed covariate's leak grows without limit as the dependence strengthens. A copula's own leak does not — it peaks at a rank correlation of 0.6 and falls. The margin of the table turns over before any cell in it does.

The correction is not a property of the sample. tr(HΩ)/q for each of fifteen candidates, at ρ = 0.7. Two candidates that fit the same number of coefficients need corrections that differ by as much as 1.49, because one of them is fitting the persistent predictors and the other is not — so no single number can be right for both, and the scalar n/n_eff = 5.537 is above every one of them. The four predictors carry persistences 0.9, 0.6, 0.3, 0; at one persistence for every column the whole spread collapses and a scalar looks exactly as good as the trace.

Counting what is independent

A penalty is a trace

Akaike's 2q is not a count of coefficients. It is the answer a trace collapses to when the rows are independent — and once they are not, the trace is still the right object and is no longer the count.

A proposal that moves more, refused more often. The two halves of the trade, both exact, on the 410 admissible assignments of twelve units. The integrated autocorrelation time of an imbalance the rule was never handed falls from 7.30 at one swap to 3.97 at three, and the acceptance rate falls with it, from 58.8% to 40.8%. A rejected proposal costs one evaluation and leaves the chain where it was, so acceptance is not the price of anything and the ranking by acceptance is the reverse of the ranking by cost. Past three the family folds: exchanging k of six from each arm is the complement of exchanging six − k, so k = 5 has the same 36 proposals as k = 1 and k = 6 has 1.

What a block may vary

A proposal that moves more than two units

The walk's autocorrelation is a fact about its step size and not about its acceptance rate. Exchanging three units from each arm mixes nearly twice as fast as exchanging one, and is refused a third more often.

The rate and the size of a disagreement

A rate times a size

A sweep reported what it costs to let every candidate choose its own tuning parameter and found it flat across the list. It was reporting a product, and the two things multiplied together do not behave the same way at all.

What each variant loses before anything has been searched for. The mean loss differential of each of the eight variants against the benchmark, over 600 tables of 60 origins, with every fit given 71 rows. The series is an AR(1) and every variant adds a lag whose coefficient is zero, so in population the two forecasts are the same forecast and the difference drawn here is estimation noise and nothing else. The marked line is σ²(q₁ − q₀)/n = -0.01408, which is an expression in how many coefficients each model has and how many rows it was fitted on — it knows nothing about the series, the persistence or which lag the variant added, and every bar is within a fifth of it. This is the amount a reference distribution recentred at each column's own sample mean believes the candidates are already behind by.

Searching among fitted models

A table of nested models

A benchmark and eight variants of it, each adding one thing. Every variant is behind before the search begins, by an amount that can be written down before the data exists — and the two most natural ways of reading the table are wrong in opposite directions.

The test, checked where the answer is known. A fourteen-unit trial at eight tolerances. At each one the admissible set is enumerated — 1534, 886, 304, 158, 126, 116, 102, 84 assignments — and its components counted, which is only possible because 3432 equal splits of fourteen units can be walked. The dots are the test, which walks none of them: two chains, one started at an assignment and one at its complement, compared on a statistic the rule was not handed. Filled marks are tolerances the enumeration says leave the set in more than one piece. The test fires on every one of them and on none of the others, 0 misses and 0 false alarms.

What a chain cannot report

A test rather than a survey

A thin admissible set falls into an arrangement and its mirror image, and the walk that samples it is uniform on half the reference distribution for ever. That was found by enumerating fourteen units, and enumeration stops at twenty-four.

The construction survives a difference of two weighted means. Coverage of δ̂ ± t√(S_D²/H) on b − 1 degrees of freedom, over 900 runs at a requirement of 0.3, where δ̂ is the block differences weighted by h_b = (1/m_A + 1/m_B)⁻¹ and H is their total. The theorem the one-mean field rests on goes through with h_b in place of the block size, and the reason is that the weights a weighted least squares decomposition needs are the inverse variances — which is exactly what h_b is. The stopping rule reads only within-arm within-block contrasts, so it is a function of nothing the interval reports, whatever it does with the block sizes. Each bar is within 2.9% of the level it claims.

A promise about two arms

A width promised for a difference

The exact fixed-width interval was built for one mean. Two arms make the target 42.7 units of effective size and each unit costs four observations, so the same promise about a difference costs 169.4 rather than 42.7 — and the theorem survives untouched with the harmonic size in place of the block size.

One zero is arithmetic and one is a symmetry. What two balancing rules remove of the interaction they are aimed at, on five joint laws of the ranks matched at a Spearman correlation of 0.4, with a normal covariate throughout. A rule holding a median split of each covariate removes exactly nothing of the product of the splits under every one of them, including the two that are not symmetric under reflection — and the reason is not a symmetry at all: a centred median split takes the values ±½, so its square is a quarter identically, and the interaction is orthogonal to both main effects whatever the joint law is. A rule holding the mean of each removes exactly nothing under the three radially symmetric copulas and 7.71% under the two that are not. Bars at the floor are exact zeros; the axis cannot draw 9e-32.

The other half of the dependence

A zero that is arithmetic

A median split's exact zero was explained by a symmetry of the latent normal. It holds under a Clayton copula, which has no such symmetry, because a centred median split squares to a quarter identically.

One zero holds and one does not. Three rules, at a correlation of 0.5, against the skewness of the covariate. A rule balancing the mean of each covariate removes exactly nothing of their product when the marginal is symmetric — including the heavy-tailed symmetric one at skewness zero, which is what says the guarantee needs symmetry rather than normality — and removes up to 29.7% when it is not. A rule balancing a median split of each removes exactly nothing of the product of the splits under every marginal here, to 1e-30: both sides are functions of the sign of the latent normal, and a monotone transformation moves neither. A rule balancing a threshold at a value on the covariate's own scale removes between 4.9% and 22.5% — it never had a zero to lose, under any marginal at all.

A guarantee that needed a symmetry

A zero that rests on a symmetry

A balancing rule removes exactly none of an interaction between two odd functions, at every correlation. The argument needs the joint sign flip to preserve the law, and no real covariate is symmetric about anything.

Two designs for one model, and the weights are not equal. Where the runs go, for the same two-parameter model at K = 1 and a ceiling of T = 10. The D-optimal design for both parameters is the familiar one: half the runs at 0.8333 and half at the ceiling. The design for the half-saturation constant alone moves the lower setting down to 0.6040 — where the response curve is still bending, which is where K is visible — and, unlike every design in the two fields before this one, it does not split the runs evenly: the weights are exactly 1/√2 and 1 − 1/√2, 0.7071 and 0.2929, at every K, V and T. The equal weights of D-optimality were a consequence of asking about both parameters at once, and nobody had to notice while that was the only question being asked.

What the design is asked to guarantee

An efficiency that is a ratio

A design chosen for a model is not a design chosen for the parameter somebody wanted. Asking for one of two parameters moves the runs, unbalances the weights, and costs the other question exactly 15.07% — at every setting, because it is algebra.

Three intervals, one shortfall. What each of three intervals actually covers, at four rules and two block windows, over 300 samples of 120 rows. All three are built from the same resamples on the same draws, so a difference between them is a difference in what is done with the resampled series. Not one of the twenty-four cells reaches the ninety-five per cent it promises. The studentised interval runs from 75.7% to 92.3%, the percentile interval — the earlier field's — from 80.0% to 89.7%, and a normal interval on the same scale from 81.7% to 89.0%. The standard repair for a percentile interval's shortfall does not repair it.

The interval, studentised

An interval that carries its scale

A percentile interval inherits the resampled distribution's skewness and its scale error together. The standard repair is one extra variance per resample. It was named and not run, so this runs 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.

Designs that change while they run

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.

Eight groups, τ = 1 against a within-group spread of 3. Each row is a group. The hollow circle is the group's own mean, the filled one is the estimate after pooling, and the small mark is the truth the data was generated from. The group of 3 moves 75% of the way to the population mean of 0.10; the group of 40 moves 18%.

Groups that borrow

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.

Every split of 100 units, σ = 1 against 3. Each point is one integer split, with its variance computed exactly rather than simulated. The minimum is at 25:75, which is the ratio of the spreads 25:75, and equal allocation costs 25% more variance — the same as throwing away 20 of the 100 units. The shaded band is every split within 5% of the best, and it runs from 17% to 35%: sharp to state, flat to sit on.

Splitting the units

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.

A charge for a covariance's own dimension

The charge nobody derived

A band of lags is charged one log-likelihood unit apiece, because that is what a regression coefficient costs. A band's numbers are not regression coefficients, and measuring what they actually cost puts the convention out by a factor of nearly three.

Four runs, and the term they cannot reach. Every run sits at a corner, so x₁² and x₂² are 1 at every run and both columns are copies of the intercept. The normal matrix is singular: the design has no information about curvature at all, and no analysis can recover it.

The surface between the corners

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 end of the family is the member the algorithm cannot reach. Every member of the Φₚ family optimised on the same 11² candidates, and two eigenvalues of each answer. The upper curve is the smallest eigenvalue of the information matrix — the quantity E-optimality maximises — which rises from 0.0993 at the D end to 0.1994 at p = 64. The lower curve is the gap between that eigenvalue and the next one up, which falls from 0.0611 to 0.0011. A smallest eigenvalue is not differentiable where it is repeated, and the family is driving the gap to zero: the one criterion here whose meaning fits in a sentence is the one whose optimum sits on a corner of its own surface. The candidate grid is on a slider and it answers a narrower question than it looks. On this square region, refining an odd grid from seven to eleven moves nothing at all — the optimum's support is the corners, the edge midpoints and the centre, and every odd grid from five up contains all of them. An even grid has no centre point and cannot reach the answer at any member of the family. On a disc, where the boundary passes through no grid point, refinement does move it.

The criterion, and what it assumes

The family behind the letters

A, D and E are not three ideas. They are three points of one family with a single dial, and running the dial from one end to the other doubles the smallest eigenvalue of the information matrix while closing the gap above it fifty-three-fold — which is the family driving its own last member to the place where it stops being differentiable.

The fourth-order expectation, by two routes. Every inner product in an eight-term slice of the dictionary at ρ = 0.5, computed from the linearisation and Mehler's formula and counted from two hundred thousand draws of a correlated pair. The entries that matter are the ones off the main effects: ⟨f(X)u(Y), g(X)v(Y)⟩ is a fourth-order expectation, which the independent-covariate field could not write down. The worst departure is 1.99 standard errors over 36 pairs, measured in each pair's own error because the entries differ in size by two orders of magnitude.

When the two are not independent

The fourth moment that was missing

Mehler's formula makes the main effects exact at any correlation and stops there, because the interactions need an expectation of four Hermite functions rather than two. A linearisation turns the four into two, and the whole geometry becomes closed again.

Where a taper's case begins

The gap a sample shows

The exact difference between two block windows at a block length of twenty is three tenths of a point. What a hundred and twenty rows report is four and a third, because the autocovariances the window is applied to are attenuated too.

What the procedure may not read

The guess with two numbers in it

Every optimal design for a non-linear model is optimal at a guess. Where the model has one parameter that moves the settings, that guess is a number and everything about it comes out in closed form; where it has two, three constants become functions and one of them becomes zero.

A quantile is the dearer reading, everywhere. The error each rule and window delivers on the two error readings, over 400 draws. The lower pair of lines is the implied long-run variance — the instrument the earlier field uses — and the upper pair is the 95% point of the standardised resampled mean, read against the finite-sample truth of 3.889 found by simulating the law directly. The quantile costs more at every one of the eight cells: at the plug-in rule it is 59.1% against 45.3% for the taper. That is not a defect in the bootstrap; a quantile is a statement about the shape of a distribution as well as its scale, and a fixed number of resamples estimates a tail worse than a variance. What matters for the comparison is that the two orderings between the windows are not the same, which the margins figure is about.

The block length read on a quantile

The instrument and the reading

Every comparison between two block windows in this collection is an error in an implied long-run variance. Nobody reads a long-run variance. Read on the 95% point a test uses, the same bootstrap costs half as much again.

A probe chosen rather than picked

The part the rule already took

A diagnostic that reports on what a balancing rule was not handed is run through a column that is 92% inside the span the rule balanced — because orthogonality in the population is not orthogonality on fourteen units.

A pair pulled back at 20% of the gap per step. Above, the two series. Below, the difference between them. The gap is pulled back towards zero by 20% of itself each step, so it stays inside a band of 14.3 while the series themselves travel much further. Nothing here is stationary except the difference. The faint line below is the gap for two free walks from the same seed, drawn for comparison.

Series that move together

The regression that is not spurious

Two random walks regressed on each other are called significantly related three times in four, so the time-series field ends in a warning. The exception it names and does not measure is here — and when the pair is genuinely tied, the fitted relation converges at rate 1/n rather than the usual 1/√n.

Twenty samples of 40, every one of them genuinely normal. Each panel is a quantile-quantile plot of 40 draws from a normal distribution. The worst point in the worst panel sits 0.87 standard deviations off the line. Anything a reader would reject here would be a false alarm.

What makes it checkable

The seed is part of the figure

Every other site in this fleet draws from a deterministic rule, so a figure either is or is not what it claims. Here the figures are samples, and a sample can be right by luck. That changes what a figure has to carry.

Six groups of 10, each fitting its own slope, then borrowing. Each faint line is one group's own least-squares slope through its own centre; each solid line is that slope after pooling towards the population slope of 0.79. Every group has the same 10 observations. The group whose x values span 0.4 has a slope standard error of 1.86 and moves 91% of the way in; the group spanning 2.0 has a standard error of 0.37 and moves 28%.

Hierarchy past one number

The slope that borrows

Pooling a mean makes it look as though how much a group borrows depends on how much data it has. Pool a slope instead and the illusion breaks — ten groups with ten observations each can borrow anything from 28% to 91%, decided entirely by where those ten observations were placed.

The same 40 units, arranged two ways. Both designs estimate the same effect of 0.5 and both are unbiased — 0.488 and 0.497. The blocked design's estimate has standard deviation 0.318 against 0.692, a variance ratio of 0.21 where the model predicts 0.20.

Decided before the data

The variance removed before the data

Arranging forty units in pairs rather than assigning them at random cuts the variance of the estimated effect to a fifth — and the fifth is knowable in advance, because it is exactly the share of the variance the pairs do not carry.

The curvature is in the denominator. The optimism a Bartlett band of each width actually costs, divided by that width, on two ways of measuring the width, over 2000 draws at 120 rows. Measured in the weights the band spends — Σ w(k), which is what the earlier field levies its charges on — the reading falls from 0.9528 at two lags to 0.7486 at thirty, so a charge proportional to the summed weights is too dear at one end and too cheap at the other. Measured in the pairs the band uses — Σ w(k)(1 − k/n), because a lag of k is an average over n − k products — the same readings are flat from 4 lags up, at 0.0084 of χ² per width against 0.2359. The correction has no fitted parameter in it: it is a function of the window, the width and the sample size.

A charge that is not a straight line

The width a band is measured in

A tapered covariance band spends 84% of its own weights at two lags and 74% at thirty. Every charge in the collection is a straight line through the origin in those weights, so it is too dear at one end and too cheap at the other.

Three series and one relation between them. Above, three series generated from Δy = Πy₋₁ + ε with Π of rank 1. Below, the combination y1 −y2. It stays inside a band of 9.5 while the series themselves travel 28.4. The count of combinations that behave this way is the rank of Π, and it is what every method in the field sets out to estimate.

Three series, and a count

Three series and a count

A pair of series is either tied together or it is not, so its whole inference is one test with one answer. Three can carry none, one or two relations at once — and the thing being estimated stops being a slope and becomes an integer, read off the gap in a spectrum whose top eigenvalue holds at 0.25 while the rest fall like 1/n.

Overlap and complementarity, separated

Two effects in one number

How much two searches over one sample share is measured as the net of two things — ground both of them find, and configurations only the joint search reaches. One extra supremum per draw separates them exactly.

Two searches over different features

Two searches that share nothing

Two searches over independent columns remove shares of the residual sum that add exactly. On the scale a chi-square point is quoted on they look super-additive by a fifth of a unit, and none of it is overlap.

Exact in the corner, where nothing was. Coverage of a nominal 95% interval on five designs, at a required half-width of 0.3. The first four are the two-arm field's own and the fifth is its corner — two variances, block sizes that swing by eight, and an allocation that alternates between five to one and one to five — where neither of that field's two conditions holds. The effective-size weights over-cover there at 98.40%; the weights h_b(λ) = (1/m_A + λ/m_B)⁻¹ cover at 94.84%, and at 94.84% when λ is estimated from the within-arm contrasts rather than known. Nothing here is supposed to move.

The weights the corner needs

Weights that need only a ratio

A fixed-width interval about a difference is exact under either of two conditions and under neither in the corner. It is exact there too, and the only thing it needs is how much larger one arm's variance is than the other's.

Coverage of four nominal 95% intervals, n = 20. Computed exactly by summing over all 21 possible counts, not simulated. The Wald interval drops to 18.2% and is jagged everywhere; Clopper–Pearson never falls below 95% and pays for it in width.

Intervals, counted

What the 95% refers to

An interval that claims 95% is making a checkable statement about a procedure, not about the interval in front of you. Build every possible sample and count, and the interval taught first turns out to cover 87.6% of the time.

weakly informative — Beta(2, 2), updated by 5 of 20. The prior is worth 4 observations. With 20 observations the posterior mean is 0.292, against a data proportion of 0.250 and a prior mean of 0.500.

The prior, doing visible work

What a prior is worth

A prior is not a philosophical position, it is a component with a stated size. For a proportion it is worth exactly a + b observations, which turns "how much does the prior matter" from an argument into a subtraction.

One forecast, and the band the arithmetic puts round it. An AR(1) with φ = 0.75, 60 observations, fitted by least squares and forecast 14 steps ahead. The point forecast decays towards the fitted mean at φ̂^h; the band is ±1.96 standard errors from σ̂²Σψ̂², which grows with the horizon and stops at the unconditional spread 1.72. The dashed pair is the same band computed at the true parameters, which nobody has. The marks past zero are what actually arrived: 12 of 14 inside the band this once, which is one draw and settles nothing.

The observation that has not happened

What the model says next

The usual account of a time series stops at estimation. A forecast asks the other question — not what the parameter is but what the next observation will be — and the band round it is a closed form that grows with the horizon and then stops growing, at a value the series was going to reach anyway.

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.

The best of a set, and what the search costs

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.

What eight groups say about τ, when the truth is 1. The posterior density for the population spread after eight groups whose standard errors run from 0.5 to 2.1. The shaded band is the central 95% interval, from 1.02 to 4.44; the posterior median is 1.99 and the mean 2.18. The vertical mark at 1.07 is the moment estimate that empirical Bayes substitutes and then treats as known.

The spread, and its own uncertainty

What the plug-in forgets

The shrinkage weight needs a population spread, and the population spread has to be estimated from eight numbers. Empirical Bayes estimates it, substitutes it, and proceeds as though it were known — and the interval that comes out covers 79% rather than the 95% it claims.

A probe from what the rule blocks

What the rule blocks

A balancing rule breaks the admissible set into pieces by refusing exchanges. Which exchanges it refuses is computable from the design and the tolerance alone, before any assignment exists — and it makes a probe.

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.

Comparing two forecasters

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.

The same covariate, three ways round. Three worlds over a treatment, an outcome and a covariate, joined by the same three edges at the same three strengths — 0.90, 0.50 and 0.70 — differing only in which way the two edges touching the covariate point. In the first the covariate causes both and adjusting for it recovers the effect of 0.50 exactly. In the second the treatment causes the covariate, the effect is 1.13, and adjusting returns 0.50 — the direct edge alone, with the part that travels through the covariate deleted. In the third the treatment and the outcome both cause the covariate, the effect is 0.50, and adjusting returns -0.087. The regression that produces those three numbers is one formula, and nothing in the data says which panel it is being run in.

What conditioning on a variable does

One arithmetic, three decisions

A covariate beside a treatment and an outcome can be a common cause of both, a step on the path between them, or an effect of both. The regression that includes it is the same arithmetic in all three, and it is right in one — returning 0.5000, deleting 0.6300 of the effect, and turning 0.5000 into −0.0872.

The tail past the last observation

Three shapes, one limit

A normalised sum has one limit and a normalised maximum has three, indexed by a single number. Twenty blocks put the sign of that number right 97.3% of the time — and naming the family from a light-tailed record gets worse as the record grows, from 83.0% at twenty blocks to 4.8% at five hundred.

The first stage an instrument needs is set by the violation nobody can see. The error each estimator converges on when the instrument has a direct effect of 0.05 on the outcome — a path the exclusion restriction asserts is zero and no sample can check. The instrument's error is δ/π exactly, so it is the reciprocal of the very quantity that made the method work: 1.0000 at a first stage of 0.05 and 0.0833 at 0.60. Least squares carries the confounding instead, at 0.3440 at a first stage of 0.30. The two cross at π = 0.1389, and the crossing is exactly δ times 2.7778 — the first stage an instrument needs is proportional to the violation it is assumed not to have, and below that line the method being corrected is the better estimator.

A variable that moves one thing only

The assumption nothing tests

An instrument buys a causal effect with an assumption no sample can check, and the price is set by the same quantity that made the method work. The first stage it needs is 2.7778 times the violation it is assumed not to have, so a direct effect of 0.05 demands a first stage of 0.1389 and least squares wins below it.

One wrong model, four designs, four slopes. The slope a straight line converges to when the truth is a quadratic, under four covariate distributions, by two routes: the population projection in closed form, and the mean of 2500 fitted slopes at 200 rows apiece. The even spread over [0, 2] gives 1.6000 and the same spread moved to [1, 3] gives 2.6000, while widening it to [0, 4] gives 2.6000 — the same number as the shifted one, because a symmetric design's target is the truth's tangent slope at the design's own mean and does not read the spread at all. An exponential spread with the SAME mean as the first gives 2.6000. So two studies of one world, each fitting the same wrong model, honestly report slopes 1.0000 apart, and neither is making an error.

A standard error for a model that is wrong

What a wrong model estimates

A straight line fitted to a curved truth converges on the tangent at its own design's mean. Two honest studies of one world, fitting the same wrong model, report 2.600000 and 1.600000, and neither is in error.

The coverage is exact and it is not the nominal rate. ⌈(m+1)(1−α)⌉/(m+1) against m, the number of calibration points, at α = 0.05. It is a closed form and needs no data. It never falls below 95.0% and never reaches 1−α+1/(m+1), the two bounds the rank argument gives. It equals 95.0% exactly at 10 of the 182 sizes drawn — the sizes where (m+1)α is a whole number, which are 20 apart — and sits above it everywhere else, worst at 38 points where it is 97.4359%, or 2.4359% of coverage nobody asked for. Below 19 points there is no such order statistic and the interval is the whole line, which is where the curve starts.

Coverage without a distribution

Coverage from exchangeability alone

A conformal interval's coverage is a fact about the ranks of m+1 numbers, so it can be enumerated before any data arrive — all 40,320 orderings of eight values, agreeing with the closed form to machine precision. What that exactness delivers is not 95%.

What each forecaster says, and what is true. The true probability of the event given a forecaster's signal, and what three forecasters report. The truth is Φ(-0.5 + 1.2w) and the honest forecaster reports it, so its curve and the truth are the same line. The loud forecaster pushes every probability towards the ends and the hedged one pulls every probability towards the middle; both have their mean report held at the base rate of 0.3744, so each crosses the truth exactly once and neither can be caught by checking its average. Their reliability terms are 0.008500 and 0.013025 against the honest forecaster's zero, and all three have the same area under the ROC curve, 0.868312.

A forecast that is a probability

An identity in three terms

Reliability minus resolution plus uncertainty is quoted as a rewriting of a probability score. It is an identity to 2.6·10⁻¹⁵ on the one grouping where reliability is the whole score and resolution exactly cancels uncertainty, and it is out by 0.004125 on the coarsest grouping anybody would actually draw.

A weight that balances, and one that unbalances. The standardised difference between the arms on each covariate, integrated over the population rather than counted in a sample. Unweighted, the arms differ by 0.8310 on the first covariate and 0.6015 on the second, which is what makes the raw difference of arm means 2.7102 against a true average effect of 1.0000. Weighting each unit by one over its own assignment probability removes both differences exactly — -2.78e-17 and -5.69e-19, which is machine precision and not a small number — because the weighted density of the treated arm is the population's own whatever the propensity is. Weighting by a score fitted without the second covariate balances the first to 0.0035 and pushes the second out to 0.7057, further apart than doing nothing.

Weighting one sample into another

A score that balances

Weighting each unit by one over its own assignment probability drives the standardised difference between the arms from 0.8310 to 2.8×10⁻¹⁷ — exactly, not nearly. A score fitted without the second covariate leaves that covariate at 0.7057, further apart than doing nothing at all.

The value that is not there

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.

8 exponential draws, standardised, against the normal. The source is one-sided and skewed. At n = 8 the standardised sum has skew 0.695, and the theory says 2/sqrt(n) = 0.707 — so the convergence is visible AND its rate is predicted.

The distribution itself

Sums of almost anything

The theorem says sums converge on one shape whatever they are sums of, which is remarkable and true. Watching it happen from a one-sided skewed source, with the rate of convergence predicted in advance, is more convincing than watching the shape appear.

20,000 p-values from a true null, n = 12. Flat, as it must be: under the null a p-value is uniform on (0,1). The Kolmogorov–Smirnov distance from uniform is 0.0090 (p = 0.81). That flatness is the check that catches an error a single rejection rate would miss.

Tests, and the second number

A p-value that is not flat is not a p-value

Under a true null, p-values are uniform. That is stronger than saying the test rejects 5% of the time, it constrains the whole distribution rather than one point of it, and it catches implementation errors that a rejection rate sails past.

A charge that is not a straight line

A lag the sample has less of

A sample autocovariance at lag k is an average over n − k products, not n. Count a band's width in the pairs it actually has and the curvature in its charge goes away, on a correction with nothing fitted in it.

A probe from what the rule blocks

A model and a count

The share of a unit's exchanges a tolerance box refuses can be modelled from the design or counted over the admissible set. They order the units the same way at a correlation of 0.81 and disagree about the level by 0.027.

Where the two kinds of cut sit. Six covariates, each a monotone transformation of the same latent normal. The vertical line at zero is where every median split sits, on every one of them, because a monotone map preserves order: the median of the covariate is the image of the median of the latent normal. The marks on the curves are where a threshold at 1 on the covariate's scale falls — 1.000, 0.881, 0.875, 0.783, 0.713, 0.337 — and none of them is at zero. That is the whole of the difference. A function of the sign of the latent normal is odd, and a rule made of odd functions removes exactly nothing of an interaction between two of them; a threshold anywhere else is neither odd nor even and removes something.

A guarantee that needed a symmetry

A split survives what a mean does not

The two things every trial balances come apart on a skewed covariate. A median split is a function of the sign of the latent normal whatever the marginal is; a mean is not, and its exact zero is gone at a skewness of one.

The shape the covariate enters by

A threshold in the tail

How much of a threshold's imbalance a balanced covariate removes is a correlation, and the correlation is a closed form. At the median it is exactly 2/π — the same 2/π a median split throws away — and two standard deviations out it is an eighth.

What a longer block buys and what it costs. A trapezoidal block at 120 rows, with the error split into the two things it is made of. The bias falls with the block length, because a longer block attenuates less, and it flattens at 23.2% because the sample's own autocovariances are short whatever window is applied to them. The spread rises with it, because a longer block means fewer of them. Their sum in quadrature has a minimum at ℓ = 16, which is not where either of the two has one. The faint line is the rectangle's total error, for scale: it is above the trapezoid's from ℓ = 12 onwards.

Where a taper's case begins

Bias is not the whole of it

A window that reaches zero at its ends attenuates less and uses less of each block. The block length that minimises its bias is not the one that minimises its error, and comparing two windows at one length compares one of them mis-tuned.

How wrong the ratio is allowed to be. λ enters only through the weights, so misstating it leaves the estimate unbiased and moves two things — the interval's calibration and its efficiency — both of which are closed forms of the design. Coverage stays at its level over a factor of two in either direction (94.93% at half the truth, 94.27% at twice it) and starts to go at a factor of five. An estimate on hundreds of within-arm degrees of freedom is never wrong by anything like that, which is what makes the feasible rule usable rather than merely definable.

The weights the corner needs

Blinded, and still exact

The one number the exact interval needs is a ratio of within-arm spreads, which is a contrast and contains no mean — so a rule forbidden to look at the effect may compute it, on more degrees of freedom than the interval itself has.

The one candidate an effective sample size is right about. n/n_eff with the finite-sample inflation Σ(1 − |k|/n)ρ^|k| is not an approximation to tr(HΩ) for a fit with only an intercept — it is that trace, to machine precision, because the hat matrix of a constant column is 1/n everywhere and its trace against Ω is the mean of Ω. The quoted limit form n(1 − ρ)/(1 + ρ) is not even right about that one. And the average correction the table's fifteen candidates actually need is 3.318 per parameter, well below the scalar, so applying it to all of them over-charges every one.

Counting what is independent

One number for a table of candidates

An effective sample size is a real quantity, it is exactly right about one thing, and that thing is a mean. Substituted into Akaike's criterion it changes nothing at all, because the penalty it is meant to fix has no sample size in it.

Ten groups of 10, pooled on the log-odds scale. Each row is a group. The hollow circle is its own proportion, the filled one is the estimate after pooling, and the vertical rule is the pooled population proportion of 31.3%. One group saw no events at all, and its raw proportion of zero becomes 21.2% — an estimate the group's own data cannot produce and the population's can. The arrows are not the same length, and none of the groups differs in size.

Hierarchy past one number

Pooling a proportion

A proportion cannot be shrunk on its own scale — an estimate would leave the interval, and how much information a count carries depends on where it sits. Move to log-odds and the approximation works, at the price of a group that saw nothing having no estimate at all until the correction supplies one.

Four designs, scored on the one parameter that was wanted. Every design scored by its Ds-efficiency for K at 13 true values across a 16-fold range. The peaked curve is the subset design built at the guess K = 1: 100% there and 42.1% at the worst point of the range. The flat curve is the maximin-Ds design, never above 64.8% and never below 61.2%. Between them is the maximin design for the pair — a robust design, protecting something else, and worth 41.9% at worst here. The lowest curve is the D-optimal design at the guess, which is what an experimenter who wanted K and looked up a design for the model would actually run: 29.1% at the worst point, against 61.2% available.

What the design is asked to guarantee

Protecting one parameter over a range

A design for a non-linear model is optimal at a guess. A design for one of its parameters over a range of guesses is a worst case of a ratio of two determinants, and it is not a special case of either problem it is made of.

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.

Stopping rules

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.

Two promises, and no rule here keeps both. A fixed-width procedure promises two things: that the interval covers at its nominal rate, and that it is no wider than the width asked for. Over 1500 runs of the modelled weighting, a rule that stops when the interval it will report is short enough keeps the width — only 2.0% of runs come out wider than 0.34 — and covers at 91.13% against a nominal 95%. A rule that stops on a width predicted from the within-arm sums of squares covers at 94.80% and comes out wider than promised on 42.3% of runs. The two promises are in conflict because keeping the second one exactly requires conditioning on the very quantity that has to be independent of the stopping time for the first.

When a fixed width is reached

Stopping on the arms

The width a trial will report is predictable from quantities the interval is not about. A rule that stops on the prediction covers at 94.5% where one that stops on the interval covers at 91.5, and it costs two blocks and half of the width promise.

Sheppard's arcsine, by two routes. Corr(sign X, sign Y) as the covariates' correlation runs from zero to one, drawn twice. One route is a sixty-four-node quadrature of the orthant probability over the correlation — the general construction, which works at any pair of cut points; the other is (2/π) arcsin ρ, which is elementary and works only at the median. They agree to 3.3e-16 at every one of 81 correlations, which is what licenses the quadrature everywhere else. The curve is above the diagonal at small ρ and below it at large: two signs agree with probability ½ + arcsin(ρ)/π, so a correlation of 0.5 gives exactly ⅓ and a correlation of 0.8 gives 0.5903.

A cut point, at a correlation

The arcsine that closes it, and the error that was overstated

Two median splits of a correlated pair agree with probability ½ + arcsin(ρ)/π, exactly. And the truncation the field was avoiding falls geometrically in the correlation, not algebraically in the order.

A budget of 4,000, at 1 and 20 a unit. Every affordable pair, enumerated. The best is 280 cheap units and 186 expensive ones — a ratio of 1.51, against the σᵢ/√cᵢ rule's 1.49. The unit rule, which says buy in the ratio of the spreads, lands at 66:197 and costs 17% more variance for the same money. Both rules are right about their own constraint; only one of them was asked.

Splitting the units

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.

A search with no fixed point

The displacement is a parameter count

A nested variant is behind its benchmark out of sample before anything is searched for. The closed form for how far turns out to have nothing about nesting in it — only two integers and a window length — and it prices a table where no candidate contains any other.

How much memory a fit takes out, candidate by candidate. Under AR(1) at 0.8, the lag-one autocorrelation a candidate's residuals report, computed exactly for each candidate on 200 draws. The upper line is the law at 0.8000. A candidate that is an intercept alone reports 0.7773 — which is exactly what a sample of 120 errors reports, because an intercept annihilates the sample mean and nothing else, and the two arithmetics agree to the last bit. Every predictor after that takes more out, down to 0.7341 at the fullest candidate. That is the collision this field is about: the rule every whitening here uses estimates its nuisance once, from the fullest candidate, so that the criteria stay comparable — and the fullest candidate is the one whose residuals report the least.

Fitted together, or fitted after

The fit that takes the memory out

A candidate's residuals report less dependence than its errors do, and how much less is arithmetic rather than noise. The rule used for a good reason reads the series that has lost the most.

What a 95% forecast interval covers, counted. 1200 series of 25 observations from an AR(1) with φ = 0.7, at each horizon, on one set of seeds. The upper line is the interval computed at the true parameters — it covers 95.3% on average, which is the check that σ²Σψ² is the right formula rather than a claim about anything a forecaster can do. The lower line is the same formula fed σ̂² and φ̂: 92.8% at one step and 87.3% at 6. The interval that would cover what it claims is 6.9% wider at one step.

The observation that has not happened

The interval that forgets it estimated

The forecast band is derived for a model whose parameters are known, and then computed by putting estimates into it. Counted, the 95% interval covers 87.3% six steps ahead on twenty-five observations, and the point forecast inside it returns to the mean a third faster than the series does.

Most of the rise is the optimiser's, and under one law it is not. The rise in log-likelihood from the tapered plug-in to the maximum over the same eight-lag band, beside what the same optimiser produces on a sample generated from the plug-in's own covariance — where the family is correctly specified by construction and there is nothing to find. Under AR(1) at 0.8 the raw rise is 5.72 and the manufactured baseline is 4.79, leaving 0.93 at 1.8 standard errors; under long memory the excess is 0.14, at 0.2. Under the moving average it is 11.87 at 19.4 standard errors, on every draw. The taper is a shrinkage, and it costs nothing where the sequence decays smoothly and a great deal where it stops dead.

A covariance with no parameter

The plug-in and the maximum

A tapered covariance estimate sits five and a half log-likelihood units below the maximum of the likelihood it is substituted into. Four fifths of that is what the optimiser would have found if nothing were missing.

Three readings, one verdict. Every tolerance of a fourteen-unit trial, with three comparisons on each. The first is between a chain started at an assignment and a chain started at its complement, which is what a mirror split separates. The second is between two chains started at the same assignment on different streams, which nothing about the set can separate — so a large reading there says the run is too short and not that the set is in pieces. The third is the same comparison on the statistic's absolute value, which is symmetric under the complement and therefore blind to the split by construction. The verdict is the pattern rather than any one line: the split is called only where the first fires and the other two do not, which happens at exactly the tolerances the enumeration calls disconnected — 0.8, 0.75, 0.7.

What a chain cannot report

The statistic that changes sign

A test for an unreachable half needs a quantity that tells one half from the other. Every symmetric reading of a mirror pair is identical, and a magnitude is the natural thing to reach for.

Where the normal approximation converges, and where it does not. Relative error against the exact binomial. At n = 1280 the error at the median is 0.96% and three sigma out it is 25.7% — a factor of 27. The tail is where the approximation is used.

The distribution itself

The tail converges last

The central limit theorem is usually shown as a shape arriving. What the demonstration leaves out is the rate — and the rate is wildly different in the middle and in the tail, which is where every approximation in the subject is actually read.

The variance touches p and never crosses it. d(x) = f(x)′M⁻¹f(x) along the diagonal of a square region, for the D-optimal measure. The line at 6 is the number of parameters in the model. Kiefer and Wolfowitz's theorem says a design is D-optimal exactly when the largest d anywhere in the region is p — not approximately, equals — so the optimal curve is tangent to that line at its support points and below it everywhere else. Here the largest value anywhere on a 41×41 grid is 6.000000000.

A design chosen rather than looked up

The theorem that says when to stop

A search that maximises the volume of the information has no way of knowing it has finished, because nothing tells it what the maximum is. Kiefer and Wolfowitz's equality does — a design is D-optimal exactly when the worst prediction anywhere in the region equals the number of parameters, which is 6.000000000059 here, gated at machine precision.

The criterion, and what it assumes

The two terms anybody wanted

D-optimality estimates all six parameters of a quadratic as precisely as possible. Nobody wants that. An experimenter looking for a maximum wants the two curvature terms, and the design that gives them is not the D-optimal one — it is a quarter of the runs at the centre, exactly, and the D-optimal design is 75.3% efficient for the question that was actually asked.

The weight on the population, σ = 3. Each curve is one population spread τ. A group's estimate moves B = se²/(se² + τ²) of the way to the population mean, where se = σ/√n is what the group's own mean does not know. At τ = 1 a group of 9 observations sits halfway.

Groups that borrow

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.

A window with two wrong ends. The regret of a rule whitened by a Bartlett-tapered Ω̂, as the window widens, against three rules that need no window at all. At L = 0 the estimate is the identity and the rule is exactly least squares — 0.08556, the same number to five places. It falls to 0.01754 at L = 20 and rises again by L = 30, because a quarter of the sample's lags are then being estimated from it. The automatic bandwidth a practitioner would reach for, 4(n/100) to the power 2/9, which at this sample size is 4, gives 0.02963 — 69% above the best available window. The rule told the dependence is an AR(1) sits at 0.01440 throughout, which is the price of not knowing the form.

Estimating the dependence, not naming it

The window that has to be chosen, and the term that was dropped

An estimated covariance has a bandwidth in it, and both ends of the dial are wrong for different reasons. The rule a practitioner would reach for is two thirds worse than the best window there is.

Four designs, and what each of them guarantees. The worst Ds-efficiency each design achieves anywhere in a rectangle of parameter values 4 times wide in each coordinate. The design built at the guess guarantees 7.3%: it is perfect where it was built and nearly useless at one corner. The D-optimal design at the same guess guarantees 25.6% — it answers the wrong question everywhere and is therefore not concentrated on being right anywhere. The third is the one this field exists to measure: maximin over the first parameter's whole range, with the second held at its guess. It guarantees 7.0%, which is no better than the design that protects nothing. Protecting both is worth 45.9%, and it needs 3 settings to do it.

What the procedure may not read

The worst case in two directions

A design that protects a range of one parameter is robust. Protect the range of one parameter while holding the other at a guess and the design is still robust, still has a guarantee, and guarantees no more than a design that protects nothing at all.

No block size is best at both things the procedure claims. Two claims and one dial. The honest interval's half-width falls as the blocks get smaller, because the interval's degrees of freedom are the number of blocks: 0.2602 at blocks of two against 0.2933 at blocks of sixteen. The fixed-width claim — that the mean is within 0.25 of the truth — gets more reliable as they get larger, because the sample size is less variable: 92.40% against 95.00%. Both are computed from the same runs, and the second is reproduced to within a tenth of a point by E[2Φ(d√N/σ) − 1], which needs the sample-size distribution and nothing else. The schedules sit at the bottom left: as narrow as the smallest fixed block and as few observations, with the rule's spread estimate on half as many degrees of freedom again.

The block size as a schedule

Two degrees of freedom, one total

The block size is a dial, and the two things a fixed-width procedure claims move in opposite directions along it. Divide the width by the square root of the sample size and one of them turns out to depend on the number of blocks and on nothing else.

Coverage of four nominal 95% intervals, n = 30. Computed exactly by summing over all 31 possible counts, not simulated. The Wald interval drops to 26.0% and is jagged everywhere; Clopper–Pearson never falls below 95% and pays for it in width.

What makes it checkable

Two routes to every number

A site about probability that only simulates has one route to each answer and no way to tell a right one from a plausible one. Every important number here is computed twice, by arithmetic that shares nothing, and the two are required to agree.

Twenty walks up the same hill, σ = 2. Each walk fits a plane to the same four-corner factorial, takes its gradient as a direction, and steps along it until a run comes in below the one before. The true optimum is the cross. 80% of the walks stop before the best point on their own path — not because the direction was wrong, but because one noisy run is enough to stop them, and the direction error costs only 3.9% of the available gain.

The surface between the corners

Walking up the gradient

The fitted gradient is wrong by an angle with a closed form, σ/(|β|√N), and what that angle costs is its squared cosine — twelve per cent at twenty degrees. What costs a third of the gain is not the direction at all. It is deciding where to stop.

Paying for a search

What a search costs in parameters

An information criterion's penalty is an estimate of the optimism a fit carries. For a break point the optimism can be measured and cannot be counted, and it comes to about two and a half parameters.

Four windows, one line, and one that is off it. The optimism measured for each window at a band of 30 lags, against what that window's weights sum to, on 2000 pairs of independent samples of 120 rows. The diagonal is where a window that spent exactly its summed weights would sit. Three of the points are one shape at three levels — the Bartlett window, its square and its cube, whose sums stand in the ratio 6 : 4 : 3 — and they lie on a line through the origin at 0.767 of the diagonal, with 0.033 between the highest and the lowest. Scaling the weights scales the charge by the factor the weights predict, which is what makes the weights the mechanism. The Parzen window has a comparable sum and a different shape, and it sits at 0.871: its weights stay near one over the first few lags, and the first few lags are where the information is. A weight sum treats every lag as equally informative and no sample does.

A charge for a covariance's own dimension

What a window leaves free

A Bartlett window's weights sum to exactly half its width, which is a candidate for what the band costs. Varying the weights without varying anything else says the weights are the mechanism; varying the shape at the same weight says they are not the arithmetic.

Overlap and complementarity, separated

What a zero is made of

Two disjoint dictionaries of independent columns read an excess of 0.000116 and are made of an overlap of 0.000583 and an interaction of 0.000467. The control the whole scale is anchored on reads zero because two effects cancel.

One curve is a binomial coefficient and the other is a line. The number of subsets a maximin over this dictionary would have to score, against the number the exchange algorithm actually scores. At three functions the walk is 2,024 subsets and is the honest answer; at eight it is 735,471 and the exchange algorithm has looked at 421. The warrant for the second curve is the four sizes where both exist and agree, which is a weak warrant — it says the algorithm has not yet been wrong, not that it cannot be — and it is the only one available past the point the first curve leaves the page.

When the set is too large to walk

Where the enumeration stops

A maximin over an eight-function dictionary is a walk over seventy subsets. Over twenty-four it is 735,471 at eight functions, and the exchange algorithm that replaces the walk scores 421. What licenses the second curve is four sizes where both exist and agree, which is a weaker warrant than it looks.

Generality in the wrong direction buys nothing. Regret on a sample whose persistence changes from 0.95 to 0.65 at row 60, over 200 draws. The three stationary rules — told one number, told a window, told an order — are within 0.4 standard errors of each other, and all three stop in the same place: they are general in the lag direction, and the departure is in the other one. Letting the model change once, at a point estimated from the same residuals, is worth 0.05021 more at 4.5 paired standard errors — about as much again as the whole of the first repair. Being told where the break is adds 0.01926, and being told the entire covariance adds 0.02465.

The shape a dependence has

Where the generality runs out

A covariance that changes half way through a sample is not one a window can estimate. One number, a window and an order are worth the same as each other on it — and letting the model change once, at a point nobody can locate, is worth as much again as all three.

A design that assumes less

Where the minimum is attained

A design that protects a range is finished when its worst case is a tie. That is a checkable property rather than a description, it is why the search cannot climb a derivative, and it is the same corner the criteria field found at the end of the Φₚ family.

The same data, one regression per choice of left-hand side. The two-step procedure has to put one series on the left, and with 3 series there are 3 ways to do it. Each returns a relation and a residual test; the 5% point is -3.71, simulated. Here they do not agree: 2 of 3 reject, and the relations they report are written with a 1 in the position of whichever series was on the left, so they can be compared. Nothing in a printed output records which regression was run.

Three series, and a count

Which series goes on the left

The two-step procedure has to pick a series to regress the others on, and nothing in its output records which. With a pair that choice never changes the verdict. With three series and one relation between them, the three choices disagree about whether the system is cointegrated at all 98.0% of the time.

The guarantee, as the basis is allowed more functions. The lower line is the best worst case over the six named shapes for a basis of each size, found by scoring every subset of the dictionary — an exact answer, since the problem is finite. One function guarantees 2.3%, which is nearly nothing; three guarantee 59.0% and the basis that does it is the covariate, its square and its cube, with no indicator in it. The upper line is the same problem with the basis drawn rather than fixed, which is worth 2.09 times as much at two functions and 1.32 at three. The two lines converge because a basis large enough to protect everything has nothing left to randomise over.

Choosing what the rule reads

Which shapes are worth protecting

Choosing a basis by its worst case is a finite problem with an exact answer. The answer has no tie in it, which a maximin optimum is supposed to have — and the tie comes back, along with twice the guarantee, when the basis is drawn rather than chosen.

A promise about two arms

Which weights are the inverse variances

There is an exact estimator when the two arms share a variance and another when every block has the same two counts, and between them they cover every trial anybody designs on purpose. In the corner where neither holds, both cover 98.45% instead of 95%, and the only estimator at its level is the one with no theorem behind it.

One distribution, two effects. Three causal structures fitted to one covariance matrix over a treatment, a covariate and an outcome. Each reproduces it exactly — the largest entry-wise disagreement across all three is 4.4e-16 — so no sample of any size distinguishes them. The regression of the outcome on the treatment and the covariate returns 0.500 in all three, to within 4.4e-16, because that coefficient is a function of the covariance and of nothing else. The effect the three worlds hold is 0.500, 0.848 and 0.848: adjusting is exactly right in the first and off by −0.348 in the other two. The arithmetic cannot see the difference and the difference is the whole question.

What conditioning on a variable does

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.

One tail arrives; the other is still on its way at a million. The Kolmogorov distance between the exact law of a normalised maximum and its Gumbel limit, at six block sizes, for two parents that both have that same limit. Both are closed form: the exact law of a maximum is F(x)^n and no simulation is involved. The exponential parent's distance falls from 0.0280 to 2.707e-7 — a factor of a hundred thousand, which is exactly one over n. The normal parent's falls from 0.0522 only to 0.0091, a factor of 5.74, because its rate is one over log n. At a million readings a block the two differ by a factor of 33556.3.

The tail past the last observation

The maximum converges slowly

The rate at which a normalised maximum reaches its limit law is computable rather than simulable, because the exact law of a maximum is always available. For a normal parent the distance falls like one over the logarithm of the block and is still 0.0091 at a million readings; for an exponential parent, with the same limit, it is 2.707×10⁻⁷.

Unrepresentative in every respect but the one that matters. Three properties of the complete cases as the chance of being observed leans harder on the regressor, in closed form, at 35.0% of outcomes missing throughout. The mean of the regressor among the rows kept climbs from 0.0000 to 0.5528 against a population mean of zero, and the mean of the outcome from 0.0000 to 0.3980 above its own. The bias in the fitted slope is exactly zero at every one of the ten settings, because selection acting on the regressor alone leaves the conditional law of the outcome given the regressor untouched and least squares conditions on exactly that. The sample is wrong about almost everything and right about the one quantity being estimated.

The value that is not there

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.

A weak instrument gives back the problem it was hired for. The counted mean bias of two-stage least squares at 4 instruments and 200 rows, over 2000 draws a setting, against the standard approximation and against the least-squares inconsistency the instrument was brought in to remove. At π = 0.02 the counted bias is 0.3220 ± 0.0142 where least squares is out by 0.3594 — 89.6% of the way back. At π = 0.3 it is 0.0118 against 0.2647. The approximation, the inconsistency over the population first-stage F, tracks the count at the weak end and sits above it in the middle: 0.968, 0.971, 0.918, 0.810, 0.740, 0.722, 0.846 as the ratio of counted to approximated bias.

A variable that moves one thing only

Weak, and back where it started

A consistent instrumental estimate at two hundred rows and a concentration parameter of 0.32 is biased by 0.3220 ± 0.0142 against a least-squares inconsistency of 0.3594 — 89.6% of the way back to the problem it was hired to solve. Just identified, it has no mean at all, and that is measured as a rate rather than assumed.

A standard error for a model that is wrong

The bread and the filling

The robust standard error is not a safety margin. At one setting of the error variance it is 1.2806 times the model-based one and at another it is 0.8246 times it, and the sign of a single dial decides which.

$Three answers to how much sample is left. What a set of inverse-probability weights leaves of the treated arm, by three routes, at six settings of the assignment rule. The integral 1/(π∫φ/e) reads the whole covariate space and falls from 0.9392 to 2.655e-3. Kish's effective size counted in samples of 600 falls only to 0.2861, because almost all of the integral's fall is in a region a sample of six hundred never draws from. And the fraction the variance of the weighted mean actually delivers is lower again — 0.1155 — because the variance is the average of one over the effective size and the effective size averaged is not the same number. At the widest overlap all three agree to 0.05%.$ Weighting one sample into another

How many observations a weight leaves

Kish's effective sample size is exact — for an outcome whose mean does not move with the covariates the weights are built from, the studentised variance reads 1.0680 where the formula says one. For the population's own outcome the same reading is 6.769, rising to 52.497.

One forecaster, one sample, and the bins it was read in. A reliability diagram of 500 forecasts in 10 equal-count bins, drawn over the curve the same forecaster has in population. The forecaster is honest, so its population curve is the diagonal exactly and every departure the points show is sampling. The sample's reliability term reads 0.002262 and its expected calibration error 0.0358, against a true reliability of 0.000000. Both are properties of this binning as much as of this forecaster: at 5 bins and at 50 the same honest forecaster reports 0.001429 and 0.014100.

A forecast that is a probability

A curve that is a binning

A forecaster with no miscalibration in it at all reads 0.001429 at five bins and 0.014100 at fifty, on the same five hundred forecasts. The closed form is K/n times the forecaster's own irreducible score, and subtracting it returns zero.

Kaplan–Meier from 120 subjects, 59 of them censored. The step curve is the estimate, the smooth curve is the truth it is trying to recover. 59 of 120 subjects were still event-free when observation stopped; they are not dropped, and they are not counted as events — they leave the risk set at the time they were last seen.

When the data stops early

The curve that survives censoring

Kaplan–Meier recovers the true survival curve to within a fraction of a point at every censoring level from 37% to 71%, where dropping the censored subjects is off by 28 and then by 43. The estimator is a running product and the reason it works is in its denominator.

One odds ratio in every stratum, and a different one marginally. Five strata with baseline risks from 5% to 85%, a treatment allocated by a coin in each, and a conditional odds ratio of exactly 2.5 throughout. The marginal odds ratio is 1.789. Nothing is confounded; the odds ratio is simply not a weighted average of odds ratios.

When the stratified answer and the pooled one disagree

The change that is not confounding

Five strata, a treatment allocated by a coin in every one, and an odds ratio of exactly 2.5 in all five. The odds ratio computed on the pooled table is 1.789. Nothing is confounded — an odds ratio is not a weighted average of odds ratios, and the risk difference, on the same table, is exactly its own stratum value.

Two studies with an R-squared of 0.85. The left study's points sit 0.50 from the line and the right study's 2.00 — a factor of 4.0. Both report an R-squared of 0.85 and, at the same sample size, the same standard error for the slope. The design was chosen to make it so, and it can always be chosen.

What a summary of a scatter is a property of

The t statistic wearing different clothes

For a simple regression, t² = (n − 2)R²/(1 − R²), exactly, on every dataset — checked to sixteen significant figures over five hundred fits. So a paper reporting R² and a p-value has reported one number twice, and two studies with the same R² have points four times further from the line.

The upper tail of 10 exponential draws: normal, one Edgeworth term, two Edgeworth terms, each against the exact tail. Each curve is an approximation divided by the exact gamma tail, so 1 is exact. Six standard deviations out at n = 10: the normal gives ×0.0000670, one Edgeworth term ×0.00159, two ×0.0167 and the saddlepoint ×1.0007.

Past the first term of the normal approximation

A correction that goes below zero

One Edgeworth term takes the normal approximation's error at two standard deviations from 38% to 8% on ten exponential draws, and stretches the range within 10% of the truth from 1.66 to 3.09 standard deviations at a hundred. It also turns negative in the short tail at every sample size — past 3.13 standard deviations at a hundred draws and 9.83 at a hundred thousand — because the region recedes only as the sixth root of n.

A near-perfect cancellation, at one correlation. A covariate skewed at 0.75 under a lower-tail copula, at each of 7 rank correlations. The earlier field measures this cell at a Spearman of 0.4 and reads 0.002% where adding the two halves' own leaks gives 16.579% — a cancellation so near exact that it is that field's headline. Across the sweep the same cell reads 0.0084%, 0.0182%, 0.0097%, 0.0015%, 0.0864%, 0.4693%, 1.5327%. Its smallest value is at 0.4, in the interior, and by 0.7 it is 1007.40 times larger. The near-zero is where two curves cross, and they cross beside the one correlation that was measured.

The same table at seven correlations

The zero that was a crossing

A cell that leaks 0.002% where adding its two halves gives 16.6% is a field's headline. On a finer grid it passes through zero at a rank correlation of 0.38 — two hundredths from where it was measured.

When the set is too large to walk

A count that has to be estimated

At sixteen units the admissible assignments can be counted by walking all 12,870 of them. At four hundred there are about 2^393.70, and the share admitted is 0.31885 against a closed form of 0.31818 that has no trial size in it at all. The exhaustion a small trial runs into is a fact about small trials.

What a chain cannot report

A defect that is about size

The admitted share of a rerandomisation barely moves with the number of units. The number of admissible neighbours grows like the square of it, and that is what decides whether the walk can go everywhere.

A line in the right width beats two curves. How far each candidate charge sits from the measured optimism across the plateau, in units of each width's own standard error, over 2000 draws. The straight line through the origin in the band's summed weights — which is what the earlier field levies — misses by 0.2382 per width. The same straight line in the pairs the band actually uses, Σ w(k)(1 − k/n), misses by 0.0095. A fitted power law misses by 0.0293 and a fitted decaying rate by 0.0172, both on one fitted constant more. The deferral this field answers asked for a curve; the answer is a line, in a variable with nothing fitted in it.

A charge that is not a straight line

A line that beats two curves

A deferral asked for a curve. Fitted against the same measurements, a straight line in a variable nobody had to fit describes the plateau better than either curve does with a constant more — and for three windows out of four it does not.

Overlap and complementarity, separated

A split that depends on the order

Run the second search first and pin that instead, and the same draw gives a different overlap and a different interaction — with the same difference. And one pair has no second order at all.

16 groups shrunk towards a fitted line, at γ = 1.2. Hollow circles are the groups' own values, filled ones the estimates after pooling, and the diagonal is the line fitted through them with each group weighted by how well it is measured — slope 1.21, intercept 0.20. The horizontal rule is where the same 16 groups would have been shrunk to with no covariate. The spread left to borrow against is 0.64 with the covariate against 1.28 without, so every group is pulled further in than it would otherwise have been.

Hierarchy past one number

Borrowing towards a line

A group shrunk towards the average of all groups is being compared with groups it has nothing in common with. Fit a group-level predictor and it is shrunk towards what the predictor says a group like it should be — which halves the spread left to borrow against and takes a quarter off the squared error.

What each criterion selects, at 50 observations. 700 series from an AR(2) with coefficients 0.6 and -0.3, every order from 0 to 8 fitted to the same 42 responses so the log-likelihoods are comparable. AIC finds the true order 55.1% of the time and lands above it 25.7%; BIC finds it 54.1% and lands above it 4.0%. The closed form for one extra lag is P(χ²₁ > 2) = 15.73% for AIC, which does not depend on n at all, and P(χ²₁ > ln n) = 4.79% for BIC at this size, which falls to zero. Under the true order is the other failure and it is BIC's: 41.9% against 19.1%.

The observation that has not happened

Choosing the order

One criterion is consistent and one is not, which is the whole of what gets said about them. At two hundred observations the consistent one is right 95% of the time and the other 70%; at fifty they are both right 54% of the time and wrong in opposite directions, and consistency has not started to mean anything yet.

Paying for a search

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.

Least squares estimates persistence low, by an amount with a formula. 3000 series of 50 observations at each persistence. The lower curve is the counted bias of the least-squares estimate of φ, and the open marks on it are −(1 + 3φ)/n, computed rather than fitted. The upper curve is the bias left after adding that quantity back, evaluated at the estimate rather than at the truth nobody has: -0.0020 at φ = 0.3, -0.0023 at φ = 0.5, -0.0039 at φ = 0.7, -0.0059 at φ = 0.8, -0.0108 at φ = 0.9, -0.0165 at φ = 0.95. The formula is a leading-order expression and it understates the bias where the persistence is nearest one — -0.0882 counted against -0.0770 predicted at φ = 0.95, which is the corner of the parameter space every one of these approximations is worst in.

Comparing two forecasters

Correcting the persistence

Least squares estimates how much a series remembers of itself as smaller than it is, at every value it can take, by an amount with a closed form. Subtracting that amount back is one line of arithmetic, and what the line costs is variance.

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.

Three series, and a count

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.

One likelihood, three answers. The concentrated Gaussian log-likelihood of one sample of 120 rows under AR(1) at 0.8, as a function of the correlation the errors are whitened at. Three rules put three different numbers on this curve. The two-step rule reads the least-squares residuals and lands at 0.7616, giving up 0.304 of log-likelihood. Iterating moves it to 0.8080 and gives up 0.002. The maximum is at 0.8044. The curve is not flat between them: what a fixed point of the residual update finds is a solution of a different equation, and the difference is the Jacobian term ½log(1 − ρ²), which grows as the correlation does.

Fitted together, or fitted after

Iterating is not maximising

Re-reading a correlation from the generalised residuals and refitting converges in seven steps. What it converges to solves the first-order condition of a sum of squares, and the likelihood has one term more than that.

What each instrument costs to read. The number of draws each instrument needs to separate a rectangular block from a trapezoidal one at two standard errors, at a block length of 20 and 120 rows — measured from each instrument's own spread on the same draws. The implied variance needs 7.0 and the 95% point needs 20.2, a factor of 2.90 at this block length. There is a closed form beside it and it does not depend on either the scale or the size of the gap: the standard error of a p-quantile is √(p(1−p))/f(q) over √B where a standard deviation's is σ/√(2B), which at the 95% point of a nearly normal reference distribution is 3.30 times as many draws for the same statement. And the quantile route needs every one of those draws resampled, where the variance route needs none.

Where a taper's case begins

Measuring a variance rather than a quantile

A resample's implied long-run variance can be computed from the sample with no resampling in it at all. A critical value cannot, and the difference is a factor of three in the draws before any of the resampling is counted.

Decided before the data

One factor at a time

Changing one thing per experiment estimates each effect from two conditions; changing everything at once estimates each from every run. The ratio is (k+1)/2 and it is exact — and when two factors interact, the one-at-a-time design recommends a setting it never tried.

A search with no fixed point

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.

The criterion, and what it assumes

The design that needs the answer

Every design this site has computed is optimal whatever the experiment turns out to say, because X′X does not contain the parameters. For a non-linear model it does, so the best place to take a measurement is a function of the number the measurement exists to find — and guessing it three times too low costs two and a half times more than guessing it three times too high.

The correction, at a generating α of -0.2. Each point is one step: the gap at the end of yesterday against the change in y today. The fitted slope is -0.202 against the -0.2 the data was generated from, which means 20% of any disagreement between y and its long-run relation with x is undone in a single step. A shock therefore has a half-life of 3.1 steps. Neither series is stationary; the relation between them is.

Series that move together

The model that corrects its error

A cointegrated pair can always be written as a mechanism — today's change in y depends on yesterday's disagreement between y and its long-run relation with x. The coefficient of that disagreement is recovered from data that never saw it — and on unrelated series the same fit produces one a t table would call real 41% of the time.

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 reference distribution the design supplies

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.

The row count entered twice, and a penalty is one place. Regret against the best available model as the errors are made persistent. Counting rows more than quadruples; both penalty repairs — the trace, and the scalar effective sample size — are worse than it at every persistence measured; and whitening the sample and keeping the ordinary penalty falls, recovering 86.9% of what counting rows gives up at ρ = 0.85. Doing it at an estimated ρ recovers 80.6%, so having to estimate the dependence from the rows being selected on costs 7.3% of what knowing it is worth. Mallows' forms are drawn beside the logarithmic ones and behave the same, which is what rules the linearisation out.

Counting what is independent

The repair that was exact and made it worse

A penalty computed from the trace is exactly the optimism it estimates, and selecting with it gives up a fifth more than not correcting anything. The row count entered the criterion twice, and a penalty is the second place.

Searching among fitted models

The weight that is a vector

Two forecasts have a best combination and one number describes it. Eight have a best combination too, and the vector describing it puts nothing at all on the forecast with the smallest mean squared error.

The shape a dependence has

The window a whitening wants

Every law here is best whitened by a window several times longer than its own memory, including the one whose memory ends at the fourth lag. The three ways of choosing it from the sample all land in the same place, and it is the wrong one.

The guarantee that survives a correlation, and the one that does not. What a balancing rule handed both main effects removes of the pure interaction between them, as the covariates become dependent. For median splits it is exactly zero at every correlation, because sign(x)² = 1: the interaction sign(X)sign(Y) is orthogonal to sign(X) and to sign(Y) whatever ρ is. For the product of the raw covariates it is 4ρ²/(1+ρ²)² — 64.00% by ρ = 0.5, rising to all of it at perfect correlation. A cut away from the median sits between them and is not small: 23.01% at a cut of one. The zero is not a fact about interactions. It is a fact about a dictionary whose functions square to a constant, which a polynomial one does not.

A cut point, at a correlation

The zero that survives a cut

A rule holding both main effects removes half of a pure interaction between correlated powers and exactly none between correlated median splits. The guarantee that a correlation destroyed was never about interactions.

What a rule reads, against what the outcome uses. The variance of the treatment estimate relative to a coin's, for four things a rule might balance against three shapes the outcome might have, over 350 trials of 200 units. The diagonal is the easy part — a rule that reads the function the outcome uses removes about half the variance. What the table is for is the off-diagonal: reading the covariate alone is worth nothing against a quadratic (0.755), and reading all three is worth nearly as much against every shape as the matching rule is against its own (0.532, 0.493, 0.514).

The shape the covariate enters by

Three functions of one number

A rule that balances the covariate is exposed to every shape the outcome might have. A rule that balances three functions of it costs two points of variance against the shape the first was built for and takes the worst case from a coin's to about half of it.

A central composite design, 13 runs. Adding 4 axial runs at ±√2 gives every factor three levels, which is the least that can estimate a squared term. The normal matrix now inverts, so each βᵢᵢ has an estimate of its own — and at exactly this axial distance the design is rotatable, which the next figure measures.

The surface between the corners

Three levels, and the ring where the design says the same thing

A central composite design puts its axial runs at ±α, and α is not a matter of taste. At F to the quarter the prediction variance depends only on how far a point is from the centre and not at all on which direction it lies in — a property with no simulation in it, exact or absent.

Scoring a search without spending data

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.

How long a walk has to be given. Every equal split of twelve units is enumerated, the 410 admissible ones are found, the transition matrix is built, and the distance from uniform is computed exactly at each step — no simulation anywhere. The walk is started at the least balanced admissible assignment, which is the state a rejection sampler is least likely to have handed it and the one a burn-in has to cover. It is 0.0849 away after twenty steps and 0.00008 after ninety. A real cost, and a small one, and naming it is what stops it being assumed to be zero.

When the two are not independent

Walking the admissible set

A rerandomisation test hunts for admissible assignments and throws away the rest. A walk visits them instead — and it is exactly uniform only because it stands still when a proposal fails, which is the step that looks like waste.

What differencing fixes, and what it costs, 100 steps. The first pair is the false-positive rate for two independent random walks: 77% on the levels, 4.9% on the differences. The second pair is how much of a real relationship survives: R² falls from 0.91 to 0.33. The same operation does both.

When the observations repeat each other

What differencing costs

Differencing takes the false-positive rate between two unrelated walks from 76.7% to 4.9%, and takes a genuine relationship's R² from 0.91 to 0.33. Applied to a series that did not need it, it doubles the variance and installs a correlation of −0.5 that the data never had.

A normal mean with a flat prior — one interval, two readings. Both intervals are [1.878, 3.446]. The frequentist reading is that the procedure captures the truth 95% of the time; the Bayesian reading is that the parameter is in this interval with probability 0.95. The endpoints are identical to machine precision.

The prior, doing visible work

Where the two schools agree

With a flat prior on a normal mean, the credible interval and the confidence interval are the same interval, endpoint for endpoint. Knowing exactly when that stops being true is more useful than either camp's general argument.

The threshold buys accuracy and spends exceedances. The mean squared error of the estimated shape against the threshold, split into the square of its bias and its spread, over 600 records of 2000 readings from a a normal parent. At the 0.9 quantile 199 exceedances are left, the bias is -0.1708, the spread is 0.0701 and the total error is 0.0341. The bias falls as the threshold rises because the exceedances get closer to being generalised Pareto; the spread rises because there are fewer of them. The sum is smallest at the 0.925 quantile, at 0.0340, of which 80.6% is still bias — so even the best threshold on this grid is one where accuracy, not spread, is the binding constraint.

The tail past the last observation

The threshold is a dial

A peaks-over-threshold analysis has one knob, and raising it buys accuracy with exceedances. For a normal parent the error is smallest at the 0.925 quantile and 80.6% of it is still bias there — and both diagnostics practitioners use to set the knob lose to a fixed 0.90 rule, one by a factor of 1.590 and one by 11.881.

A filled value is not an observation. What a 95% interval for the slope actually covers after each way of handling 35.0% missing outcomes, counted over 4000 studies of 200 rows. Dropping the incomplete rows covers 95.93%. Filling with the observed mean covers 13.85%, because the estimate itself has moved. Filling with a fitted value covers 80.85% against a closed prediction of 79.73%: the estimate is right and the reported standard error is short by a factor of 0.6567 against a predicted 0.6500, because the residual sum of squares is divided by the whole sample's degrees of freedom. Adding residual noise recovers the spread and covers 85.78% against a predicted 84.62%, since the interval still ignores the variance of having imputed at all.

The value that is not there

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%.

One promise, kept on average and inside neither group. What each calibration scheme covers inside each of two equally common groups whose noise scales are 1 and 3, over 6000 draws with 200 calibration points. One interval for everybody covers 100.00% of the quiet group and 90.66% of the noisy one, averaging to 95.28% — and the closed form for that population says 99.9999% and 90.0001% at a half-width of 4.9346, from two normal cdfs and no simulation. Dividing by an estimated per-group scale gives 95.29% and 95.48%; calibrating separately inside each group gives 95.49% and 96.01% against a closed-form expectation of 95.4645%. Only the last of those is a guarantee rather than a repair, because the rank argument runs inside each group.

Coverage without a distribution

Marginal is not conditional

One exactly valid interval covers 100.00% of a quiet group and 90.66% of a noisy one, and the floor is arithmetic rather than a measurement — a group of share π is guaranteed only 1 − α/π, which is zero when the group is as rare as the miss rate.

Robust, at the sample sizes it is reached for. Counted coverage of five 95% intervals for a slope, at six sample sizes, under an error variance leaning towards the edges of the design (γ = 0.8), over 20000 draws at the small end. The model-based interval sits at about 87.06% everywhere and does not improve with the sample, because it is a claim about a variance it is not estimating. The robust ones do improve: HC0 covers 88.73% at 20 rows, 92.70% at 50 and 94.93% at 1,000. Its promise is asymptotic and its use is not, and the gap between those two facts is this picture. The leave-one-out correction read against a t on n − 2 is the only line that is near its promise at the small end: 94.55% at 20 rows.

A standard error for a model that is wrong

Robust is not free

A robust standard error's promise is asymptotic and its use is not. Its 95% interval covers 88.73% at twenty rows, and under mild heteroskedasticity it is the worse of the two intervals until a hundred.

Weighting one sample into another

The region with no comparison

A trimmed interval covers the average effect over everybody 90.8% of the time at six hundred rows and 41.0% at nine thousand six hundred, while covering the average effect over the units it kept 94.3% and 96.0% throughout. An interval that gets worse as the sample grows is an interval about something else.

One cohort of 40, and two intervals around the end of its curve. A single simulated study of 40 subjects with exponential survival at rate 0.35, dropout at rate 0.15 and follow-up to 6 — the first seed from 8811 upward whose plain band reaches below −0.05, chosen to show the failure rather than its frequency. The step curve is Kaplan–Meier and the smooth curve the truth. The plain band, the estimate plus and minus 1.96 Greenwood standard errors, first dips below zero at t = 3.78 and reaches −0.052; early on it also rises to 1.023, above one. At t = 5 the estimate is 0.069 with 1 subject still under observation, the plain interval runs from −0.052 to 0.191 and the log-log interval from 0.006 to 0.251, against a truth of 0.174. The log-log band is built on a scale that cannot leave [0, 1], and it bends away from the edge rather than through it.

When the data stops early

The interval at the end of the curve

The interval most software prints around a survival curve covers 89.7% at five years, where 3.3 of forty subjects are still being watched and where the curve is actually read. The same variance carried on a log–log scale covers 94.8% there — and the failure was never the width.

The interval that over-covers when the instrument fails. Counted coverage of two nominal 95.0% intervals for the same causal effect, read off the same 2000 draws of 200 rows at each first stage. The exact Anderson–Rubin set covers 95.3% at every setting — flat, because the statistic it inverts is built from y − tβ, which contains no π at all, and is therefore the same number on the same draw whatever the instrument is worth. The conventional interval covers 99.1% at π = 0.02 and 95.6% at π = 0.6: it goes wrong at the weak end by covering too MUCH, at a median width of 7.320, because its standard error is computed from residuals taken at an estimate that has itself gone wrong. A weak instrument does not make this interval lie about its coverage; it makes it useless while telling the truth.

A variable that moves one thing only

What the first stage does not know

A single weak instrument does not make the conventional interval undercover — it makes it cover 99.1% at a width of 7.320. Where the promise actually breaks is many instruments — coverage falls from 97.2% to 51.5% while the median width falls from 1.454 to 0.583.

Forty O'Brien–Fleming trials at a true effect of 0.16, with the boundary written as an effect. The dashed line is the smallest effect a trial can report and still stop at each look: 0.510 at 80 observations, 0.255 at 160 observations, 0.170 at 240 observations, 0.128 at 320 observations, 0.102 at 400 observations. The true effect is 0.16, so at 3 of the five looks a trial cannot stop without reporting more than it. 29 of these forty trials stop before the last look, each marked where it stopped.

Stopping rules

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.

How many observations the smallest and largest of them need. The interval between the extremes of n draws holds at least 95% of the population with probability 1 - n p^(n-1) + (n-1) p^n, whatever the population is. Reaching 95% confidence takes 93 observations.

The interval that holds observations, not a mean

Ninety-three observations, and nothing assumed

The interval between the smallest and largest of a sample holds a share of the population whose distribution does not depend on the population — Beta(n − 1, 2), for anything continuous. Buying the 95/95 that normality buys at ten observations costs 93 of them, and that number is the exchange rate between an assumption and data.

The upper tail of 10 exponential draws: normal, two Edgeworth terms, saddlepoint, each against the exact tail. Each curve is an approximation divided by the exact gamma tail, so 1 is exact. Six standard deviations out at n = 10: the normal gives ×0.0000670, one Edgeworth term ×0.00159, two ×0.0167 and the saddlepoint ×1.0007.

Past the first term of the normal approximation

An approximation built at the threshold

The saddlepoint approximation reads the tail of a sum of five exponential draws to within 0.19% six standard deviations out, where the normal is short by a factor of more than sixty thousand. It is within 2.2% out to ten standard deviations on a single draw, where there is nothing to average, and within 1.1% on a binomial whose expected count is one. It works because it is built where the tail is read rather than at the mean.

One t interval with its scale read three ways, 120 rows in blocks of 32. What a 95% t interval for the mean of a first-order autoregression at 0.7 covers, and how wide it is, when its block-means scale is read from the 3 disjoint blocks of 32 rows, from a block at every one of the 89 starting rows, and from those overlapping blocks tapered — over 8,000 draws. Disjoint: 94.4% at a width of 1.560, with a multiplier of 4.30. Every starting row: 94.8% at 1.054, multiplier 2.74. Tapered: 95.0% at 1.020, multiplier 2.57.

A block, weighted inside itself

A block at every starting row

The t interval on the block count reads its scale from the disjoint blocks, three of them when 120 rows are cut into blocks of thirty-two, and throws away the other eighty-six blocks the series contains. Reading a block at every starting row leaves the scale's attenuation where it was — the two expectations agree to within a hundredth at every cell — and nearly doubles the degrees of freedom it realises, so the interval loses a third of its width at the same coverage. Where the interval falls short, at short blocks, it falls short by the same amount however the blocks are read.

The best of a set, and what the search costs

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.

A wrong weight costs width; a random weight costs level. Five weightings on a trial whose variance ratio drifts by a factor of 20.1 between the first block and the last, over 4000 runs. The rule that knows every λ_b covers at 95.1% and sets the width. One ratio for the whole trial is wrong for every block and costs nothing in level — 94.8% — while being 20% wider; equal weights are calibrated by an identity and 22% wider. The ratio estimated inside each block is the only rule aimed at the quantity that actually varies, and it is the only one that misses the level, at 92.0%: a weight computed from a handful of degrees of freedom is mostly noise, and noise in a weight is not a wrong weight. Modelling the drift across blocks recovers the oracle's width at 94.8%.

What a block may vary

A ratio that changes between blocks

A wrong weight costs width and a random weight costs level. The rule aimed at the quantity that actually varies is the only one that misses its own coverage, and the rule that models it across blocks recovers the whole of what knowing it is worth.

A guarantee that stops being a number. The worst case of each dictionary over six outcome shapes, at a correlation of 0.5, against the skewness of the covariate. Under a symmetric marginal every rule made of odd functions has a worst case of exactly zero, and the rule holding a mean and a median split of each covariate — the two things every trial balances — is one of them. Under skew that zero becomes 0.74%, 1.83%, 2.24%, 2.49%: small numbers, each of which depends on a marginal nobody stated. The guarantee has not improved by becoming positive. It has stopped being a guarantee, because it can no longer be written down without the covariate's distribution in it.

A guarantee that needed a symmetry

Balancing a skewed covariate

The worst case of the rule every trial runs goes from exactly zero to somewhere between a quarter of a per cent and two and a half. Which is small, and is a number that cannot be stated without the covariate's distribution in it.

One of them is mostly leverage. How much of the design's own leverage direction each active-set probe carries, once both are standardised and projected off the rule's span — which is what a probe is, so it is the comparison that matters. Over 189 designs the modelled active set agrees with leverage at |r| = 0.8359 ± 0.0114 and the counted one at 0.4239 ± 0.0216. So the modelled probe is largely leverage under another name and the counted one is genuinely a different direction — and the counted one is the worse probe, at 0.3854 of alignment against 0.4272. What the active set contains beyond leverage points away from where the set splits.

A probe from what the rule blocks

Counting it exactly does not help

If a modelled active set lost because the model was crude, the exact one would win. It is computed at a cost no trial can pay, and it is worse — so the approximation was never what was costing the probe.

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.

Estimating the dependence, not naming it

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.

Power at an effect of 0.5 standard deviations. The curve is the non-central t on 2n − 2 degrees of freedom with δ = d√(n/2); the dots are 4,000 experiments run at each size. Reaching 80% power needs 64 per arm.

Decided before the data

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.

Adding a run can make the design worse. The D-efficiency of the best N-run design at each size, against the optimal measure. It is not a rising curve. 13 runs reaches 99.77% and 14 falls to 99.44%, because the optimal weights are real numbers and N runs is an integer approximation to them, so how good a design can be depends on how well N divides. A Wald interval behaves the same way: a larger sample sometimes makes its coverage worse, for exactly this reason.

A design chosen rather than looked up

The design that has to be integers

The optimal design is a set of real weights and an experiment is a set of runs, so the theory's answer is never available. Thirteen runs reach 99.77% of it and fourteen reach 99.44% — adding a run makes the design worse per run, and the search that finds it does not always find the same one.

Counted coverage of two 95% intervals, over 2,000 datasets. Each point is one of the eight groups, at its own standard error. The integrated interval covers 95.2% overall against its stated 95%; the plug-in covers 78.8%, and its shortfall grows with the group's standard error — from 86.1% at se 0.5 to 77.0% at se 2.1. The mean widths are 3.48 and 2.66.

The spread, and its own uncertainty

The interval that integrates

A credible interval for one group in a hierarchy has to average over every value the population spread might take. That averaging is what makes it cover — 95.2% against the plug-in's 78.8% — and it costs 31% more width, a heavier tail, and a mixture rather than a normal.

Where the maximum is, from 15 runs. One dataset, one fitted quadratic, and two answers to "where is the best setting". The delta method reports 0.80 ± 0.46, a finite interval it will report whatever the data does. Fieller's set is 0.49 to 1.76, because the curvature here has t = -4.04. The true optimum is at 0.75.

The surface between the corners

The optimum is a ratio, and its interval is sometimes the whole line

The best setting is −b₁/2b₂: a ratio of two estimates whose denominator is a curvature the design can often barely see. The delta method reports a finite interval every time and covers 68.8% where the curvature is weak; Fieller's set covers 95% and says so by being unbounded.

Four sequences, and the rule only ever sees the last one. Under long memory at d = 4/9, four things that are all called the dependence. The law itself is the top line. What a sample of 120 rows reports on average is the second, computed exactly: subtracting a sample mean takes the first lag from 0.800 to 0.538. What a candidate's residuals report is the third, lower again at 0.472, because a fit removes dependence along with signal. The autoregressions are fitted to that third sequence and reproduce it exactly out to their own order — the Yule–Walker equations are solved to make it so — so everything they say past that is extrapolation. At the twentieth lag the law has 0.576, the residuals report 0.006, and an AR(8) extrapolates 0.028.

The shape a dependence has

The order the tail is drawn at

A fitted autoregression reproduces the sample exactly at the lags it was fitted on, so everything it says past them is extrapolation — and the order is the dial that decides how much of it there is.

The allocations this trial could have made, and the ones it could not. One 120-patient trial allocated by minimisation at p = 1, re-randomised 399 times. No outcome is redrawn anywhere in this figure: each re-randomisation runs the rule again over the same patients in the same order with the same recorded factors, so what is drawn is the set of experiments that could have happened. The bars are that set; the outline is what shuffling the labels gives, which is the reference distribution of a coin and is what every off-the-shelf permutation routine assumes. The coin's is wider — its 5% point is 1.95 against the rule's 1.09 — because a coin's allocations are less balanced and a less balanced allocation gives a larger statistic. Reading this trial against it makes the test conservative rather than anti-conservative, which is the opposite error from the outcome-adaptive case and for the same structural reason.

Balancing on what was recorded first

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.

The normal density at sigma = 1.00. The bands hold 68.27%, 95.45%, 99.73% of the mass. Those figures are integrals of the curve drawn, not the memorised 68-95-99.7.

The distribution itself

The shape, and where its mass is

68, 95, 99.7 is recited more often than any other set of numbers in the subject. They are integrals of a specific curve, they are worth computing rather than remembering, and the third one is the one people misuse.

Expected width against coverage, n = 30, p = 0.15. The Wald interval is the shortest and covers 94.2%. Clopper–Pearson covers 98.3% and is 13% wider. Shortness is not a virtue on its own — an interval of zero width is the shortest of all.

Intervals, counted

The shortest interval is the one that misses

Four intervals for the same data, with their widths and their coverage measured together. The narrowest is the one that fails its stated level, which is exactly why it looks the most appealing.

The one zero neither half of the dependence can touch. A median split's interaction leak at all 30 combinations of copula and marginal, on a log scale. Every one is under 10⁻¹⁶ and the largest is 1.74e-20, which is the quadrature's own noise rather than a leak. The reason is arithmetic and it is short: a centred median split takes the values ±½, so its square is a quarter identically — for every unit, on every draw, whatever the covariate's scale is and whatever joint law the ranks have. The interaction is then orthogonal to both main effects by construction, and there is nothing for either half of the dependence to break. Both of the fields this one joins report this zero holding under their own variation; running both variations at once is what establishes that it is not two coincidences.

Both halves of the dependence at once

The zero that survives both

A median split's interaction leak is under 10⁻¹⁶ at all thirty combinations of copula and marginal. It is the only guarantee in the collection that neither half of the dependence can touch.

What 20 clusters of 20 correlated observations do to a 95% interval. Each study has 400 observations arranged as 20 clusters of 20. The lower points are the counted coverage of the usual interval, which treats them as 400 independent observations; the curve through them is 2Φ(1.96/√deff) − 1 with deff = 1 + 19ρ, computed before any data was drawn. At ρ = 0.81 the interval covers 36% rather than 95%. The upper points treat the cluster as the unit and need no variance components at all.

Hierarchy past one number

Two levels at once

A third level of grouping adds no new arithmetic and produces one number — the design effect — that decides how many independent observations a clustered study is worth. It is the same quantity the time-series field computes for autocorrelated data, arrived at from a completely different picture.

The scale moves the width; the curve does not. The band width each charge picks, averaged over 150 draws of 120 rows. The two conventions — a unit a lag and half a log n a lag — pick 6.08 and 3.65 lags. The four charges derived from the measured optimism pick 15.05, 15.60, 15.47 and 15.44, against a best width on the draw of 14.13. So the scale a charge is levied on moves the width by a factor of 4.27 and the shape of the charge moves it by 3.6%. None of the six is an estimate of the draw's own best width: the correlations are -0.006, -0.003, 0.017, -0.001, 0.016, -0.004.

A charge that is not a straight line

What a better charge buys

Four charges derived from the same measurements pick band widths within six per cent of each other and deliver errors within two per cent of the gap any of them leaves. The scale a charge is levied on decides the width; the shape of the charge decides nothing.

Fitting them together is worth something under one law. Four fits of the same regression under four dependences: least squares, the two-step plug-in every whitened rule in this collection runs, the coefficients and the band maximised together, and a whitening at the law's own covariance that nobody has. Under the moving average — the one law the band family contains — the joint fit beats the two-step by 0.0077 at 3.3 paired standard errors. Under the autoregression, long memory and the break it is a tie: 0.4, 1.0, 0.3 standard errors. That is the same ordering the likelihood gap gave, arrived at through the coefficients rather than through the objective.

A covariance with no parameter

What fitting them together buys

Maximising over the coefficients and the covariance together beats the two-step under one of four dependences and ties under the other three. It is the one the band family contains, and the likelihood said so before any coefficient was compared.

What the exactness costs, and the dial it is bought with. The median half-width of the interval each rule reports, at a requirement of 0.4 and a first look after 5 observations. The flat line is the interval a practitioner writes at the purely sequential rule's stopping time, which covers 91.72% rather than 95%. The curve is the blinded rule, which covers its nominal level at every block size: it reads b − 1 degrees of freedom where the other reads n − 1, and pays for the exactness in width. The best block size is 3, at 0.4712. Larger blocks give the stopping rule a better estimate and the interval a worse one, and the two costs go opposite ways, which is what puts the minimum in the middle.

What the procedure may not read

What the blindfold costs

The exactly-covering rule pays for it in the width of the interval, and the block size is a dial between two costs that run in opposite directions. And on an interval whose width was fixed in advance, the same repair buys nothing at all.

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.

The reference distribution the design supplies

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.

Every equation's adjustment speed, and the one number they make together. Each series gets its own equation, each is regressed on the same lagged disequilibrium, and what comes back is the whole vector α. Averaged over 400 systems at n = 300: α₁ = -0.154 against -0.15 generated, α₂ = 0.104 against 0.1 generated. The gap closes at the combination of them rather than at any one entry — 25% of any disagreement per step, a half-life of 2.41 steps, where the single equation that fits only the first series reports 4.27.

Three series, and a count

Which series does the moving

“y adjusts towards x” and “x adjusts towards y” are different mechanisms with identical long-run relations, and a single-equation model cannot tell them apart because it only writes one equation. Writing all of them recovers a vector — and a gap that closes at 25% a step where one equation alone reports 15%.

One penalty, read along two dials. How much wider the studentised interval is than the percentile one, at every sample size and every block length on the grid, with the number of whole blocks each cell leaves written beneath. Read across a row and the block length changes; read down a column and the sample size does. The penalty is nearly a function of the block count alone: the cells at 15 blocks read 1.16, 1.20, 1.17, 1.15, 1.13, 1.10 across three sample sizes and three block lengths, while the cells at one block length read anything from 1.10 to 3.95. The largest penalty on the grid is 3.95, at the cell with 3 whole blocks in it.

The interval, studentised

The count or the length

A block length and a block count are one number read two ways at one sample size. Read at three, the studentised interval's width penalty tracks the count — with an R² of 0.9911 against a closed form that has no length in it — and its coverage tracks the length.

The record stops here, and the curve does not. The level exceeded once in T blocks, against T, for a normal parent at 365 readings a block. The truth is closed form — the block maximum's own distribution function is Φ(x) raised to the 365, so the T-block level is Φ⁻¹ of the 365-th root of (1 − 1/T), with nothing fitted in it — and the fitted mean over 800 records of 50 blocks sits on top of it, 4.0186 against 4.0330 at 100 blocks. What moves is not the level but its error, which grows from 0.0956 at 10 blocks to 0.6383 at a thousand while the level itself moves only from 3.4421 to 4.5454. The rule marks the largest reading an average record contains, 4.0062: everything to the right of where it crosses is read from a fit rather than from data.

The tail past the last observation

A level with no data in it

The largest of fifty block maxima is a 51-block event by its own plotting position, so a hundred-block level is read 1.96 times past the longest event the record contains — and it lands above the largest reading on 52.4% of records. The estimate stays nearly unbiased out there; what grows is its error, sixfold from ten blocks to a thousand.

What conditioning on a variable does

A collider before the treatment

A covariate measured before the treatment, on no causal path, and not a common cause of anything, still biases the estimate by exactly −0.2000 against an effect of 0.5 — while the regression that leaves it out is exact. The bias saturates at 0.3536, and the two paths that make it a collider do not appear in that bound.

The extra 1/m, and the correction nobody quotes. What a pooled 95% interval covers against the number of imputations, counted over 2000 studies of 200 rows at 35.0% of outcomes missing. Rubin's rules — total variance W̄ + (1 + 1/m)B, read against a t distribution on (m − 1)(1 + W̄/((1 + 1/m)B))² degrees of freedom — cover 94.10% at two imputations and reach their promise by 5, at 95.25%. Dropping the (1 + 1/m) factor takes two imputations to 93.10%; using a normal quantile instead of the degrees-of-freedom correction takes it to 92.55%; dropping both takes it to 91.45%. The median degrees of freedom at two imputations is 12.95, which is why the second correction is the larger.

The value that is not there

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.

Four numbers, and only one of them is the question. Four quantities in a population where the effect is not the same for everybody: 40.0% compliers, 25.0% always-takers and 35.0% never-takers, with the compliers carrying an effect 1.0000 larger than everybody else's. The population average effect is 0.5000. The compliers' average effect is 1.1000. A valid instrument converges on 1.1000 — the second of those, not the first, and the two differ by 0.6000. Comparing the treated with the untreated as they stand gives 1.4182, wrong by 0.9182 in the same direction, because always-takers start 1.5000 above never-takers before any treatment happens. The instrument removes the selection and changes the question at the same time, and only one of those is reported.

A variable that moves one thing only

Whose effect it is

With a perfectly valid instrument and no violation of anything, the estimate converges on 1.1000 where the population average effect is 0.5000. The gap is exactly θ(1 − p_c), the always-takers and never-takers cancel out of both halves of the ratio, and five per cent defiers move the answer to 1.2667.

A standard error for a model that is wrong

Three corrections and a leverage

On an even design of twenty rows the four robust corrections read 0.8603, 0.9559, 1.0000 and 1.1647 of the truth and the choice barely matters. Add one point at x = 8 and they read 0.3191, 0.3419, 1.0000 and 5.1127.

Either model is enough; neither is not. The bias of three estimators of an average effect of 1.0000, over 600 samples of 600 units with the assignment rule at strength 1, in each of the four cells made by getting each nuisance model right or wrong. The wrong model in both cases is one that omits the second covariate, which the outcome and the assignment both depend on. The outcome model alone is off by 0.8064 whenever it is the wrong one; weighting alone is off by 0.8190 whenever the propensity model is. The augmented estimator built from both is off by -0.0085, -0.0083 and -0.0016 in the three cells where at least one of them is right, and by 0.8118 in the fourth — which is between its two components rather than better than either.

Weighting one sample into another

Either model, but not neither

The augmented estimator's bias is −0.0085, −0.0083 and −0.0016 wherever one nuisance model is right, against components off by 0.8064 and 0.8190. One step past the overlap sweep it is the least biased estimator on the table at 0.0857 and the worst on it at 1.9265.

Two groups, a baseline and a follow-up, and nothing happening in between — baseline reliability 0.6. 600 units in two pre-existing groups whose true means are 1.00 apart, read once at baseline and once at follow-up, with no change for anybody. The two groups' mean changes are −0.075 and −0.032, so the change-score analysis reports a group difference of 0.043. The regression of follow-up on baseline and group reports 0.409, against a closed form of (1 − λ) × 1.00 = 0.400: at any one baseline reading the two groups' lines sit that far apart, because each group's units regress towards their own group's mean. The pooled slope in this sample is 0.614, the baseline's reliability.

Reversals that are not errors

Two analyses of one baseline

Two groups read at baseline and again at follow-up, with no change for anybody. Subtracting the baseline reports a group difference of −0.0014 and adjusting for it reports 0.4008 — and each analysis is exactly right about one reason the groups started apart and wrong by 0.40 about the other.

Two worlds, one Kaplan–Meier curve, two truths. World A gives each subject a frailty with mean one and variance 1, and multiplies both its event hazard (0.35) and its dropout hazard (0.5) by it, so the subjects likeliest to leave are the ones likeliest to fail. World B has independent event and dropout times whose hazards are world A's crude hazards. Kaplan–Meier over 1000 studies of 400 gives the same curve from both — 0.7750 and 0.7763 at t = 1; 0.6627 and 0.6641 at t = 2; 0.5924 and 0.5932 at t = 3; 0.5047 and 0.5042 at t = 5 — and that curve is world B's truth, 0.5052 at t = 5. World A's truth is 0.3636 there. The dashed lines are the two bounds that assume nothing, from every dropout failing on leaving (0.1905 at t = 5) to none ever failing (0.6667).

When the data stops early

A dropout the data cannot see

Two worlds leave the same record to the last detail a study can write down — the same times, the same share ending in the event, the same share leaving first — and a log-rank test between them rejects at its own 5% level at every sample size from a hundred to sixteen hundred. Kaplan–Meier converges on 0.5052 at t = 5 from both. The truth is 0.5052 in one and 0.3636 in the other, and what is left to argue about is where between two bounds to stand.

Which samples Wilson and Clopper–Pearson each cover, n = 50, p = 0.2. Each bar is the probability of one count, shaded by which interval built on that count contains 0.2. Both cover 95.1% of samples, only Wilson 0.0%, only Clopper–Pearson 1.6%, neither 3.3%. The correlation between their hits is 0.810, so on shared draws the variance of their difference is 4.891 times smaller than on independent ones.

What makes it checkable

The same draws for both methods

Two intervals computed on the same simulated datasets give a difference in coverage whose variance can be 4.891 times smaller than on separate datasets — or, for a pair that covers different samples, 1.164 times larger. Which one a comparison gets is an exact sum over the counts each interval covers, and a standard error that ignores the sharing covers 100.00% for one pair and 93.07% for the other.

A forecast that is a probability

A score that rewards lying

An absolute-error score pays a forecaster exactly ⅛ of a point to replace a true quarter with a zero, and over two hundred records a liar beats a truthful forecaster on 200 of 200. A skill score against the forecaster's own average buys 0.012633 of reported skill for 0.002035 of real score.

Ordered stagewise: the outcomes at least as extreme as stopping at 160 observations with z = 3.3. Each column is one look of an O'Brien–Fleming trial; above the boundary a trial stops there. Highlighted are the outcomes that count as at least as extreme as the observed one when outcomes are ordered stagewise: at 80, z ≥ 4.56 (probability 2.54 × 10⁻⁶ with no effect); at 160, z ≥ 3.30 (probability 4.82 × 10⁻⁴ with no effect); at 240, none; at 320, none; at 400, none. The two-sided p-value is 9.69 × 10⁻⁴.

Stopping rules

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.

The fixed-width trial's coverage when the outcomes are not normal, for both stopping rules. normal: stopping on the arms 94.05% after 18.1 blocks, on the report 89.95%; log-normal, skewness 0.95: stopping on the arms 94.70% after 18.5 blocks, on the report 90.80%; log-normal, skewness 2.26: stopping on the arms 94.15% after 19.3 blocks, on the report 90.25%; log-normal, skewness 4.75: stopping on the arms 94.45% after 18.7 blocks, on the report 90.50%; t, five degrees of freedom: stopping on the arms 94.35% after 18.3 blocks, on the report 90.30%; skewness 4.75, arm A only: stopping on the arms 93.80% after 26.0 blocks, on the report 89.90%; skewness 4.75, arm B only: stopping on the arms 93.60% after 14.2 blocks, on the report 89.95%; equal variances, normal: stopping on the arms 94.75% after 11.4 blocks, on the report 90.90%; equal variances, skewness 4.75: stopping on the arms 94.05% after 11.1 blocks, on the report 92.00%.

When a fixed width is reached

A width rule on skewed outcomes

The blinded fixed-width rule rests on a within-arm spread being independent of the arm means, which only normal samples guarantee. On outcomes with a skewness of 4.75 the independence fails and the overall coverage barely notices — 93.60% to 94.70% across every shape counted, against 94.05% on normal outcomes. What skew moves is the runs that stop by twelve blocks, which cover about 90% with the skew in one arm, and the trial's length: a variance ratio corrected on normal theory lengthens it from 18.1 blocks to 26.0 with the skew in the first arm and shortens it to 14.2 with the skew in the second.

What a companion with a known expectation can remove from the variance of a simulated 5% rate. For a rate of 0.05, a companion used linearly removes at most 22.4% of the variance however well it correlates. At a correlation of 0.9 it removes 18.1%, the companion's own rate at the same cut 38.2%, and the best function of the companion 48.1%; at 0.99, 21.9%, 77.0% and 82.8%. The companion's rate overtakes the linear companion at a correlation of 0.64.

A cut point, at a correlation

A rate needs a rate beside it

A simulated rejection rate is an average of indicators, and a companion with an exactly known expectation can remove at most φ(c)²/p(1 − p) of its variance when it is used as a straight line — 22.4% for a 5% rate, 7.2% for a 1% rate — however closely it tracks the statistic. The ceiling is the share of a normal's information a cut keeps. Used as its own rate at the same cut, the same companion removes 38.2% at a correlation of 0.9 and 77.0% at 0.99. On the t test's size for lognormal data it was worth 1.43 times the draws used linearly and 2.32 times used as a rate at a matched level.

Coverage against block length, 120 rows. The coverage of the t interval for the mean of a first-order autoregression at 0.7 on 120 rows, at every block length on a fine grid, with its scale read from the disjoint blocks and from a block at every starting row, over 8,000 draws. The squared-error length for disjoint blocks at the true persistence is 13.9 rows, and the same algebra for the overlapping scale gives 16.0, marked. The overlapping interval first reaches 95% — to within a tenth of a point — at blocks of 32 rows, where it covers 94.9% at a width of 1.056; at the overlapping squared-error length it covers about 92.5%.

A block, weighted inside itself

A length chosen for the interval

The squared-error rule for a block length weighs the scale's bias against its variance. Rebuilt for a block at every starting row, whose variance is two thirds as large, it asks for blocks fourteen per cent longer and buys four tenths of a point of coverage. A t interval has already paid for the scale's variance in its multiplier, so its own coverage is predicted by the bias alone — within seven tenths of a point up to blocks of twenty-eight rows — and a rule that chooses the shortest length that prediction says will cover asks for blocks two and a half to three times longer and lands within about a point of 95% at 120, 240 and 480 rows. The price is width, and it is paid where the series is short.

A cut walked from the median into each tail. What a rule balancing a threshold on each of two normal covariates removes of the interaction between the two thresholds, with the cut moved from the 1st percentile to the 99th, on five copulas at a Spearman rank correlation of 0.4. Every copula reads exactly zero at the median. The three radially symmetric copulas are mirror images about it: the Gaussian peaks at 19.49% near the 95th percentile and is down to 13.44% at the 99th; the Frank peaks at 13.22% near the 85th and falls to 2.06%; the t is still near its highest, 37.45%, at the 99th. The Clayton climbs to 56.37% at the 1st percentile, in the tail its dependence is in, and never passes 5.39% in the other; its reflection is the same curve turned round.

The other half of the dependence

A cut walked into the tail

Move a balancing rule's threshold off the median and the interaction it leaks rises from exactly zero — and then either turns back to nothing or climbs to a ceiling, depending on one property of the dependence. With both covariates cut, the whole regression collapses to two probabilities, and far out it settles on 2λ/(1 + λ) of the tail-dependence coefficient: 57.25% under a Clayton, 35.57% under a t, and zero under a Gaussian or a Frank however strongly the covariates are related.

Overlap and complementarity, separated

The split at the critical value

Split the over-charge of two searches at the joint statistic's 95% point rather than at its mean, and the two components behave differently. The interaction — what only the joint search can reach — stays within two units of its average at every level up to the 95% point. The overlap climbs from nothing to most of the over-charge, on two searches over independent columns as much as on searches that share ground. At the critical value the split's overlap has stopped meaning shared ground: it is mostly the arithmetic of adding tails, and the identity that defines it hides that.

The table swept along the covariate instead. What a rule holding a mean of each covariate fails to remove of their interaction, at each of 4 copulas, as the covariate is skewed further and the rank correlation is held at 0.4. The sweep runs from a symmetric covariate at g = 0 to a skewness of 11.16, and the three settings the earlier table names — g = 0.3, 0.6 and 0.9 — are on it, where this sweep reproduces that table to the last digit. Every row rises and then falls: the lower-tail copula from 7.707% through 0.0015% and back to 5.587%, the upper-tail one to a maximum of 36.213%. So the quantity a trial is exposed to is not monotone in how skewed its covariate is.

The same table at seven correlations

The other dial

The table is swept along the strength of the dependence and never along the shape of the covariate. Swept along the shape at a fixed correlation, the same two copulas cross, the same way — and the near-zero cell turns out to be a minimum in both directions at once.

Where the bias lands. The drift in the log variance ratio, fitted across 12 blocks over 4000 trials. E[log λ̂_b] is log λ_b plus ψ(k_B/2) − log(k_B/2) − ψ(k_A/2) + log(k_A/2), which depends on nothing but the degrees of freedom — so the tempting sentence is that it goes into the intercept and leaves the slope alone. It does not, because the blocks alternate between allocations and the alternation is correlated with the covariate being fitted: the lopsided blocks carry 0.5383 of bias and the even ones carry none. Uncorrected the slope reads 1.5597 against a truth of 1.5, which is 8.0 standard errors. Subtracting the two digammas block by block leaves 1.4976.

What a block may vary

The bias that lands in the slope

The bias in a log variance estimate depends on nothing but its degrees of freedom, so it goes into the intercept — unless the degrees of freedom alternate with the design, which is exactly what a block-randomised trial makes them do.

The ceiling a multiplier cannot reach past. A wild-type resampling forms e*_t = e_t·w_t with the multiplier independent of the residual, so what comes out has autocovariance γ_resid(k)·γ_w(k) — the residuals' own, multiplied by the multiplier's. Since |γ_w| ≤ 1 the reference distribution's dependence is bounded above by the residuals', and the residuals' is already below the errors'. The two shortfalls compose. For a block of ℓ the multiplier's autocorrelation is exactly the triangle (1 − k/ℓ)⁺, drawn here as the dashed prediction against the realised resamples at ℓ = 5; the bound is attained only at ℓ = n, where the reference distribution is built from one sign.

Counting what is independent

What a multiplier cannot keep

Two reasons were named for the quarter a blocked resampling falls short, and taking either away makes the gap larger. What is left is a bound — a multiplier can only take dependence out, and the residuals' own is already below the errors'.

A charge that is not a straight line

What the correction assumes

A correction with nothing fitted in it repairs one window of four. The reason is that its size is set by where a window puts its weight and the curvature it must repair is set by something else — and for one window at one sample size the two happen to agree.

The tail past the last observation

Two intervals for one return level

Two 95% intervals read off the same fits of the same records, against a level known in closed form. The symmetric one covers 80.3% at twenty-five blocks and reaches only 89.0% at two hundred — and 99.24% of its misses are the interval sitting entirely below the truth, which is not the endpoint anybody expects to fail.

$The damage does not stay in the term that was left out. Where each coefficient lands when the model that fills the missing outcomes and the model that analyses them disagree, over 1500 studies of 200 rows at 35.0% missing and 20 imputations. An imputer that omits a covariate the analysis fits attenuates that covariate's coefficient by exactly the missing fraction — -0.1405 counted against a closed -0.1400 — and pushes the coefficient it did impute on the other way by exactly the product of the omitted coefficient, the covariates' correlation and the missing fraction: 0.0402 counted against 0.0420. Both closed forms come out of the same two-by-two solve. Matching models leave both alone, and so does an imputer that knows more than the analysis.$ The value that is not there

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.

Tests, and the second number

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.

Two far rows, and the line with one of them deleted. Twenty clean points and two rows near x = 9. The slope is −0.511 with every row, −0.376 with one far row deleted, and 0.495 with both deleted. Deleting one of them barely moves the line, because the other is still there.

Regression, and what the summary hides

Two points that hide each other

One far observation among twenty-one has a Cook's distance of 24.1. Put a second beside it and the two read 0.966 and 0.772, neither crossing 1, while together they reverse the slope and deleting both moves the fit by 53.3.

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%.

What makes it checkable

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.

Estimating a weight you already know is worth doing. The variance of an inverse-probability estimate weighted by a propensity fitted from the sample, over the variance of the same estimate weighted by the true propensity, paired on the same 500 samples of 600 units at each of five settings. Every reading is below one: the stabilised estimator keeps 27.8% of its true-weight variance where the assignment is nearly a coin toss and 72.0% where it is nearly decidable, and the unstabilised one 30.0% and 49.3%. Neither estimator is materially biased, so this is a variance rather than a trade. The true weights are right about the population and know nothing about the draw; the fitted weights are the value that sets this draw's own imbalance to zero, and that imbalance was what the variance was made of.

Weighting one sample into another

The estimated weight is the better one

The propensity is known exactly here, so it can be weighted by — and estimating it from the same data and weighting by that gives a variance ratio of 0.4769 on paired draws. The reason is a projection: the draw's own imbalance explains 56.33% of the true-weight variance and 0.05% of the estimated-weight one.

The squared estimate 1 standard errors from the flat point, exact and linearised. At δ = √n·μ/σ = 1 the exact law of the squared estimate has mean 2.00, variance 6.00 and skewness 2.177; the delta method's normal has mean 1.00, variance 4.00, no skewness, and 30.85% of its mass below zero, where a square cannot go. The Kolmogorov distance between them is 0.3085.

The distribution itself

Where the derivative is zero

The delta method reads a standard error off a tangent line, and at a flat point the tangent says the spread is zero. The interval built on it for a squared mean covers 99.991% there and 85.978% one and a half standard errors away, with nearly every miss on the same side — and the law it should have used is a χ², not a normal.

Four intervals at 3 blocks of 32 rows. What four 95% intervals for the mean of a first-order autoregression at 0.7 cover, and how wide they are on average, at 120 rows cut into 3 whole blocks of 32, over 240 draws with 200 resamples each under the rectangle. The normal interval, the block-means variance with 1.96, covers 82.1% at a width of 0.708. The percentile interval covers 82.1% at 0.632 and the studentised one 90.4% at 2.495. The fourth resamples nothing: it is the normal interval with 1.96 replaced by Student's t on 2 degrees of freedom, and it covers 94.2% at 1.555, 0.62 times the studentised interval's width.

The interval, studentised

The interval with no resampling in it

Replace 1.96 in a normal interval on the block-means variance with Student's t on one fewer degrees of freedom than there are whole blocks, and resample nothing. Across twenty-four cells it covers at least as often as the studentised bootstrap interval at every one, by 0.42 to 10.42 points; it is narrower wherever seven blocks or fewer are left; and at fifteen blocks of 32 it covers 95.0%, which no resampled interval on the grid reaches.

Two 95% intervals for 2 of 20, under Jeffreys — Beta(½, ½). The equal-tailed interval runs from 0.0214 to 0.2839 and is 0.2625 wide; the shortest interval runs from 0.0093 to 0.2540 and is 0.2447 wide. Both hold 95% of the posterior, and the shorter one buys its 6.8% by moving its lower endpoint towards the denser side.

The prior, doing visible work

The shortest interval, and the one that does not move

Two 95% intervals come out of every posterior and they are not the same set. The shorter one is shorter by 4.86% on average and 22.41% at its best, it covers 86.72% where the other covers 95.68%, and it is not even the shortest once the parameter is written a different way.

$What a 8-run fraction of 4 factors confounds. The defining relation is I = ABCD, so the resolution is 4. A is estimated as A + BCD; B is estimated as B + ACD; C is estimated as C + ABD; D is estimated as D + ABC. Each of those is an identity about the design rather than an approximation about the data.$ Decided before the data

The word a fraction costs

A half fraction estimates each main effect as an exact sum of that effect and everything it is confounded with — no error term, no sample-size argument. With every interaction at 0.8 the design reports a true effect of −1 as −0.20, and the design cannot test the assumption that makes the number mean anything.

What visiting fewer settings costs, 6 parameters. Carathéodory's bound puts the support of an optimal measure between 6 and 21. 6 settings: D-efficiency 88.90%, G-efficiency 57.18%, 0 degrees of freedom for lack of fit; 7 settings: D-efficiency 94.54%, G-efficiency 61.22%, 1 degrees of freedom for lack of fit; 8 settings: D-efficiency 95.99%, G-efficiency 64.60%, 2 degrees of freedom for lack of fit; 9 settings: D-efficiency 97.40%, G-efficiency 82.76%, 3 degrees of freedom for lack of fit. The saturated design has none, and buying the first one costs about five points of efficiency to get back.

A design chosen rather than looked up

How many places a design goes

Carathéodory's bound puts an optimal design's support between six and twenty-one settings, and every design in this field that can fit the model visits exactly nine. The count is not a choice anybody makes, it decides how many degrees of freedom are left to check the model with, and the first spare setting costs six points of efficiency to get back.

What 240 observations are worth, by which question is asked. 8 rows and 10 columns with 3 observations in each cell — 240 in all, each belonging to one row and one column, neither nested in the other. the overall mean: variance 0.1703 against a naive 0.0060, a design effect of 28.4 and 8.5 effective observations; a difference between two rows: variance 2.0682 against a naive 0.0960, a design effect of 21.5 and 11.1 effective observations; a difference between two columns: variance 1.0845 against a naive 0.1200, a design effect of 9.0 and 26.6 effective observations.

Hierarchy past one number

Two groupings that cross

Pupils belong to a school and to a neighbourhood, and neither is nested in the other. There is then no design effect: the overall mean is worth 8.5 independent observations out of 240, a row difference 11.1 and a column difference 26.6, and which grouping matters depends on the question rather than on the study.

What a corrected critical value delivers: actual size over nominal, upper tail, sum of 30 exponential draws. At a nominal 1% the upper-tail test's actual size is ×1.703 of nominal with the normal critical value, ×0.991 with one Cornish–Fisher term and ×0.998 with two. At 10⁻⁸ they are ×464, ×1.418 and ×0.932.

Past the first term of the normal approximation

The same correction, inverted

One skewness term added to a tail probability keeps a sum of a hundred exponential draws within 10% of the truth out to 3.09 standard deviations. The same term used to move the critical value instead keeps the test's actual size within 10% of nominal out to 5.10 — a level of about one in six million. In the short tail it has a flaw of its own: below a level of about one in a million at ten draws the corrected critical value turns back, and a test asked for a level of 10⁻⁷ rejects 1,149 times too often.

A cut point, at a correlation

A companion cut into many

A simulated rate can be estimated within bands of a companion whose distribution is exact, and the bands weighted back by their exact probabilities. One band boundary at the target's threshold is the companion's own rate; infinitely many are the best any function of the companion can do, which for a 5% rate at a correlation of 0.9 removes 48.1% of the variance. Eight bands placed where the target's conditional probability is changing remove 46.8%; eight at equal probabilities remove 29.9%, and need thirty-two to catch up. On the lognormal t test's size, thirty-two bands of the logarithms' t statistic were worth 2.99 times the draws and two hundred and fifty-six, 2.14.

A lean, its reflection, and none. The mean error of each weighting's estimated difference at a fixed eighteen blocks, 2,000 trials a shape, with two standard errors. normal: the modelled ratio, every block 0.0031, the modelled ratio, each block left out 0.0028, the modelled ratio, cross-fitted halves 0.0023, the true ratios 0.0037; skewness 0.95: the modelled ratio, every block 0.0092, the modelled ratio, each block left out -0.0134, the modelled ratio, cross-fitted halves -0.0014, the true ratios 0.0002; skewness 2.26: the modelled ratio, every block 0.0166, the modelled ratio, each block left out -0.0298, the modelled ratio, cross-fitted halves -0.0042, the true ratios -0.0029; skewness 4.75: the modelled ratio, every block 0.0255, the modelled ratio, each block left out -0.0455, the modelled ratio, cross-fitted halves -0.0055, the true ratios -0.0051.

When a fixed width is reached

A weighting that does not read its own spreads

On skewed outcomes a block's spreads move with its means, so a weighting fitted to every block's spreads leans: +0.0255 at a skewness of 4.75. The obvious repair — fit each block's weight with that block left out — does not remove the lean. It reverses it and nearly doubles it, to −0.0455, because a weighted mean divides by the sum of the weights and every other block's weight still reads the one left out. Splitting the trial into two halves and weighting each by the other's fit does remove it: −0.0055, indistinguishable from the weighting told the true ratios, for a spread about a tenth wider.

Both halves of the dependence at once

A median with ties

The median split's interaction zero survives every marginal and every copula, because a split that is on for exactly half the units squares to a constant. A covariate measured on a few levels cannot be split exactly in half: on a five-point scale three in eight units sit on the median, and a rule balancing 'above the median' removes 6.39% of the interaction under a Gaussian copula and 10.06% under one of the two Claytons. The size is set by the share of units on the median, which is the formula's own factor. And a fair coin for the tied units restores the zero exactly, on every copula.

A threshold read along the skew. What a rule balancing a threshold at the value 1 on each covariate's own scale removes of the interaction between the thresholds, against the covariate's skewness, on five copulas at a Spearman rank correlation of 0.4. Gaussian: 16.41% with no skew, 10.07% at a skewness of 11.16; t on four: 22.18% with no skew, 12.11% at a skewness of 11.16; Frank: 13.19% with no skew, 10.14% at a skewness of 11.16; Clayton: 5.33% with no skew, 4.82% at a skewness of 11.16; Clayton turned over: 33.34% with no skew, 17.61% at a skewness of 11.16. Every leak falls, because the value moves towards the median.

The same table at seven correlations

Where the skew puts a threshold

The field read the mean-balancing rule along a sequence of skewness and left the threshold rule — a cut at a fixed value on the covariate's own scale — unread. Read, it turns out to be no new curve. Skewing the scale moves the value 1 from the 84th percentile of the latent covariate to the 74th, and the rule's leak is the copula field's cut sweep read at that quantile: it falls on every copula, from 16.41% to 10.07% under a Gaussian. Whether skew and dependence compound or cancel is then a fact about the slope of each copula's curve, and unlike the mean rule's, no cell changes its answer along the sequence.

Choosing what the rule reads

What the ellipse spends its assignments on

Rerandomising on Mahalanobis distance never runs out of assignments, where a box of per-function tolerances does at four functions. But at the same number of admissible assignments it holds the worst named function half as tightly, because it spends its constraint on a combination of the basis nobody named.

When the set is too large to walk

A basis drawn rather than chosen

On two covariates no fixed basis of one or two functions protects every shape an outcome might have — its worst case is exactly zero. Draw the basis at random from the right mixture and the guarantee is a fifth of a shape for every function. The price is per trial — at three functions, two draws in five leave one shape wholly unprotected.

A block, weighted inside itself

A share read off the sample

A block length chosen for an interval's coverage needs the share of the mean's variance the scale will find, and the published rule reads it from a first-order autoregression at the sample's lag-one value. Reading it from the sample's own autocovariances instead was supposed to survive series nobody had modelled. At 120 rows it covers 92.5% to 93.5% on all four laws — worse than the wrong shape on every one — because a centred series' autocovariances sum to exactly zero and the share they imply is too generous; read to lag forty it covers 84%. The assumed shape costs width, not coverage: 17% too wide where dependence stops at lag four, and nothing visible under a break, where the interval covers for a reason the share knows nothing about.

Four intervals for the effect, minimisation at p = 0.8, 120 patients. Under minimisation at p = 0.8, 120 patients, over 600 trials with an additive effect of 0.45 and 199 re-run allocations per trial, the average width of four 95% intervals for the effect, and how often each covers it: unadjusted t interval 1.229 wide, covering 99.7%; unadjusted, test inverted 0.816 wide, covering 95.3%; adjusted t interval 0.723 wide, covering 96.0%; adjusted, test inverted 0.722 wide, covering 96.2%.

Balancing on what was recorded first

The interval the test inverts to

A randomisation test of no effect becomes an interval for the effect by testing every value at once: subtract the hypothesised effect from the treated outcomes and ask the same question again. Because the rule reads only covariates, one set of re-run allocations answers every value. Under minimisation the unadjusted t interval covers 99.7% at a width of 1.229; the inverted test of the same unadjusted difference covers 95.3% at 0.816, a third narrower, with no model of the outcome. Under complete randomisation the two are the same interval — which is what says the third was the rule's.

A search with no fixed point

The displacement on a heavy tail

A correct candidate with one more parameter is behind out of sample by a closed-form amount, and the closed form rests on one Gaussian fact: the expected leverage of a fresh row is q/(R − q − 1). On predictors that are not Gaussian it becomes whatever the leverage is, and two routes that share no arithmetic agree on what that is. With a finite fourth moment it barely moves — 1.5% more per parameter at eight degrees of freedom, 4.5% at five, 7.3% on an exponential. At three degrees of freedom it is 28% more, and the estimate of it will not settle: four batches of twenty thousand draws disagree by more than a quarter.

What the two-regime residue was made of, persistent first. Under a break in the persistence at row 60 of 120 (0.95 then 0.65), the selection regret of six whitenings over 200 draws: restart, unscaled, residual persistences 0.04043; restart, unscaled, persistences given 0.03488; restart, unscaled, fitted with the line 0.03466; the law's recursion, residual persistences 0.03856; the law's recursion, fitted with the line 0.01640; the law's own covariance 0.01579. The whitening that restarts at the break and does not rescale its two regimes gives up 0.01910 against the oracle even when it is given the true persistences; the law's recursion, which divides each row by its regime's innovation scale and continues across the break, is the oracle when given them and within 0.00061 of it when they are fitted with the regression.

The shape a dependence has

The residue was the weights

A regression whose errors change persistence at a known row was whitened as two autoregressions and still gave up 0.0246 against the law's own covariance. That residue was put down to estimating the two persistences from residuals, and the repair named was to fit them with the line. Fitting them with the line moves the persistent regime's estimate from 0.81 to 0.89 and recovers a fifth of the residue — exactly what being told the true persistences recovers. The rest was the transform: it never divided the two regimes by their own innovation scales, which differ sixfold. The law's own recursion, told the persistences, is the oracle to machine precision; fitted with the line, it estimates the persistent one at 0.945 and comes within 0.0006 of the oracle.

Where a taper's case begins

A model against a window

A block resample's long-run variance is attenuated by its window, and the construction that escapes the window is a model: fit an autoregression and sum its dependence to every lag in closed form. Measured on both halves of the answer, the escape is narrower than it looks. Correctly specified, on 120 rows of a first-order autoregression, the model's error is 45.5% of the truth against the trapezoid block's 42.4% — it removes the bias and buys a spread larger than the bias was — and it pulls ahead only from about 480 rows. Wrongly specified, on a five-period moving average, it is off by 84% to 105% at every length, and even an order chosen by the criterion trails the window throughout.

What the procedure may not read

A variance that follows the response

Every design for the two-rate compartmental model assumed the same noise at every sampling time. Let the noise grow with the response, as a combined additive and proportional error does, and the design for the slow rate runs to the tail of the curve, where the response and so the noise are smallest: at three additive standard deviations of proportional error at the peak, the constant-noise design is worth two thirds of the right one. The earlier essay expected a weight function to break the model's scale invariance. A variance that follows the response leaves it exact to six decimals; only one that follows the clock breaks it. And tailoring the design to the noise makes it more fragile to the rates: its worst case over the rectangle falls from 9.2% to 3.3%.

When the two are not independent

The share a sample removes

A rule balancing eight main effects of two independent covariates removes exactly none of their interaction — in the population. A trial is a sample, and in a sample of a hundred units exact balance on the same eight functions removes 24% of the interaction's variance on average, between 10% and 42% from one trial to the next. At twenty-five units it removes 62%. The zero is the centre of nothing: it is the limit the in-sample share falls towards, by about two fifths with every doubling of the trial, carried there by an interaction whose spread grows with the very functions it is regressed on. At a correlation of a half the closed form says 64%; a trial of a hundred gets 69% on average and anything from 53% to 83%.

A guarantee that needed a symmetry

A share at a hundred units

On a skewed covariate the closed form credits a rule that balances the means with removing 26% of the covariates' product and 52% of a square, shares that rest on symmetry having failed. A trial does not collect them. At a hundred units the rule removes 12% of the product and 37% of the square on the clearly skewed covariate, and at four hundred units barely more, because the shares live in the long tail and the tail is a handful of units. On the most skewed covariate the rule removes a fifth of the median split at a hundred units and nothing of it at four hundred: balancing the mean of such a covariate is balancing its largest few values.

Scoring a search without spending data

A penalty that counts independent rows

Akaike's penalty charges a fit two error variances a coefficient because each coefficient is fitted from n independent rows. When the design and the errors both persist, a row is worth less than a row, and the honest charge is twice the coefficient's variance inflation. On a hundred and twenty rows at persistence 0.7 that charge is 34.7 against an optimism counted at 34.5, where Akaike's charges 10. Charged it, the criterion's regret at 0.95 falls from 0.128 to 0.032 with the persistences given and to 0.065 when they are read off the sample — and at 0.5, where the charge is right and Akaike's is half of it, Akaike's still selects better.

A design that assumes less

A bootstrap that repeats the design

After a design that chose its settings from the data, a parametric bootstrap can keep the settings the experiment ran or repeat the whole procedure from the start. On twelve runs repeating it changes coverage by a point at most, because the adaptivity was nearly free. What matters is the interval's shape: the percentile bootstrap covers 90.6%, no better than the Wald interval's 91.3%; the studentised one 93.0%; the profile interval 94.9%. And after a design stuck at a twelvefold wrong guess, the studentised bootstrap — the textbook repair — covers 77.8%, with intervals averaging 54.5 wide for a parameter of 3.

Overlap and complementarity, separated

A tail the law gives the pair

Split the over-charge of two searches at their critical value and the interaction — the configurations only the joint search reaches — stays near its average while the overlap climbs. That held under one law. Under a five-period moving average and under long memory it holds for every pair in the order the field reads, to within three units. In the other order, one pair acquires a tail of its own: with the window searched first and the break second, the interaction under long memory climbs from 2.0 at the median to 7.9 at the 99th percentile, four times its average.

A leak read off a cohort, at two cuts. The threshold rule's leak as a cohort of 1,000 units estimates it from its own two-by-two table: the bar is the middle eighty per cent of 600 cohorts' plug-in estimates, the open circle their median and the stroke the true leak, for five copulas at a Spearman rank correlation of 0.4. At the 90th percentile the estimate is centred on the truth and its middle eighty per cent spans about fourteen points: Gaussian 12.8% to 26.4% around 19.2%, t on four 21.5% to 35.7% around 28.9%, Frank 5.4% to 18.7% around 12.2%, Clayton 0.8% to 9.6% around 4.4%, Clayton turned over 35.9% to 49.5% around 43.1%. At the 99th it is not centred on anything: Gaussian 13.1% to 100.0% around 13.7%, t on four 17.5% to 72.9% around 37.4%, Frank 14.4% to 100.0% around 2.2%, Clayton 16.1% to 100.0% around 0.6%, Clayton turned over 37.0% to 75.7% around 56.3%, because on three of the five copulas between two cohorts in five and four in five have nobody past both cuts.

The other half of the dependence

A leak read off a two-by-two table

The share of an interaction a threshold-balancing rule leaves alone needs one number from the data: how often a unit past the cut on one covariate is past it on the other. A cohort of a thousand estimates it to within a dozen points at the 90th percentile. At the 99th most cohorts have an empty cell in their table, and every one of those reads a leak of exactly one hundred per cent — a reading the bootstrap then confirms with an interval of zero width.

What iterating the band is worth. How much lower the prediction error is when the Bartlett band is iterated to its fixed point than when it is read once off the least-squares residuals, paired on the draw, with two standard errors, 300 draws at 120 rows for each law and window. First-order autoregression: 4 lags 2.84 ± 0.36, 8 lags 3.43 ± 0.58, 20 lags 4.16 ± 0.80; five-period moving average: 4 lags 2.04 ± 0.28, 8 lags 2.69 ± 0.42, 20 lags 4.32 ± 0.68; long memory: 4 lags 0.83 ± 0.14, 8 lags 1.13 ± 0.25, 20 lags 1.33 ± 0.44 thousandths. Every one is below zero by more than two and a half standard errors; the gain is largest at the widest band under the two short-memory laws.

Fitted together, or fitted after

A fixed point with no likelihood under it

A tapered band of autocovariances has no likelihood to maximise, so the one rule that can fit its dependence together with the regression is to iterate: read the band off the residuals, refit, read it again. It converges on every draw, in seven to eleven fits at the median, gives back about half the memory the first fit took out of the residuals under a short-memory law, and lowers prediction error by two to four thousandths — five to eight paired standard errors. Under the law a first-order likelihood describes, its maximum still wins; under the two it does not, the band's fixed point beats it.

What the main effects cost the rest of the model. The compound optimum of α·log Ds(main effects) + (1 − α)·log D on an 11-by-11 grid of the square, at 14 weights from α = 0 to 0.999, placed by its D-efficiency against the D-optimal design and its main-effect efficiency against the factorial. The D-optimal design (α = 0) gives the main effects 74.3% of what the factorial gives. At α = 0.5 the design keeps 94.6% of D and gives 85.6%; at 0.9, 64.9% and 96.8%; at 0.99, 31.3% and 99.7%. The factorial itself (open, at the left edge) gives the main effects everything and the model nothing: its D-efficiency is zero. The design optimal for the two quadratic terms (red) gives the main effects 50.0% at a D-efficiency of 83.6%.

The criterion, and what it assumes

A subset the model cannot use

Nominate the two main effects of a quadratic response surface as the parameters of interest and the optimal design is the 2² factorial — four corners, a quarter each — which leaves the full model's information matrix at rank four of six and the curvature with nothing at all. That is why the field's algorithm would not converge on it. Approached through a compound criterion instead, the trade is explicit: 96.8% of the main effects' best information costs the model 35% of its D-efficiency, and the last three points cost nine tenths of what is left about the curvature.

Which window each reading prefers. The difference between the tapered and the rectangular window, in points, on five readings at four rules: for the two errors a negative number favours the taper, and for the two coverages a positive one does. implied, variance: 1.5, 4.5, -1.1, -2.1. 95% point, uncentred: -6.1, -3.2, -7.1, -6.1. 95% point, centred: 0.9, 3.5, -0.8, -1.0. coverage, uncentred: 5.0, 2.5, 5.8, 4.0. coverage, centred: -1.2, -3.2, 1.0, 0.0. The two uncentred readings favour the taper throughout, and they are the only ones that disagree with the variance.

The block length read on a quantile

A shrink towards the answer

This line of essays reported that the 95% point is a dearer reading than a variance, that a further point wants a shorter block, and that a taper beats a rectangle on what a test reads where a variance says the opposite. All three came from one uncentred quantile. Read about the resamples' own mean, the point costs 28.5% against the variance's 45.8%, every level wants about the same block, and the windows order alike on all readings. The taper's coverage had a separate cause: its resampled mean is 0.875 of the sample's, and every series here had a true mean of exactly zero.

Student's t on 5 degrees of freedom, against the normal. The two-sided 95% critical value is 2.571 for t(5) and 1.960 for the normal — 31% wider. Using the normal at this sample size makes every interval too short by that much.

Intervals, counted

The correction for not knowing the spread

The t distribution exists because the standard deviation is estimated rather than known. At eight observations, using the normal instead makes every interval 12% too short — and the coverage that follows can be measured rather than argued about.

The covariate the treatment caused, and what it hides. A covariate on the causal path: the treatment causes it and it causes the outcome, so the treatment's total effect of 1.130 runs partly through it. Adjusting for it returns the direct edge alone, 0.500, which is what somebody wanting the total effect should not have asked for. The dashed variable is the second problem: an unmeasured cause of both the covariate and the outcome. It does not touch the treatment, so the unadjusted regression still recovers 1.130 exactly. It does touch the covariate, so once the covariate is conditioned on the treatment and the outcome are linked through it, and the adjusted coefficient lands on 0.050 — neither the total effect nor the direct one.

What conditioning on a variable does

The variable the treatment caused

Adjusting for a covariate the treatment caused stops estimating the total effect and starts estimating the direct one. When that covariate shares an unmeasured cause with the outcome it estimates neither: the total effect is 1.1300, the direct effect is 0.5000, and the regression returns 0.0500.

The exceedances arrive together. 300 steps of a max-autoregression with dependence 0.75, drawn on a logarithmic scale because its marginal has no variance. The rule marks the 0.9 quantile: 30 of the 300 readings are above it and they fall into 5 clusters, the largest holding 11. The mean cluster holds 6.000, and its reciprocal — 0.167 — is the runs estimator of the extremal index, whose true value for this process is exactly 1 − 0.75 = 0.25. Every threshold method in the collection assumes exceedances are independent pieces of information; here 30 of them are 5.

The tail past the last observation

The clustering the tail has

Every threshold method counts exceedances as though they were independent pieces of information, and in a dependent series they arrive in clusters. Ignoring that overstates a return level by the reciprocal of the extremal index — ×3.527 counted where the mean cluster holds four — and leaves a reported standard error 2.151 times too small.

$An estimate reported as a function of an assumption. What the slope really is, against a shift in the outcomes nobody saw — line from the closed form, dots counted over 2000 studies of 200 rows at 35.0% missing. Every point on this line produces exactly the same observed data, and the complete-case estimate is the flat line at 0.5996 regardless. The truth moves at -0.2845 per unit of shift, which is a function of the missingness model and the missing fraction and of nothing that can be estimated: across the swept range the true slope runs from 0.8845 to 0.3155, a span of 0.5691 against a value of 0.60 in the world where the shift is zero. Reporting the line is the honest form of the answer.$ The value that is not there

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 rows are held fixed; only the clusters move. Counted coverage of four 95% intervals for a slope, at five cluster counts with the row count held at 300 throughout and a within-cluster correlation of 0.1, over 6000 draws apiece, with the sizes equal. The interval that counts rows covers 53.42% at 5 clusters — a second closed form says 2Φ(z/√D) − 1 = 54.44% for a design effect of 6.900, and reads nothing about clusters at all. The cluster-robust interval read against a normal covers 74.43% there and 94.20% at 100 clusters; read against a t on G − 1 it covers 85.08% and 94.47%. The number of independent things is the cluster count, and every quantity here is blind to how many rows were typed.

A standard error for a model that is wrong

The count that is not the rows

Three hundred rows in five clusters of sixty carry 6.9000 times the variance an independent-rows calculation reports, and the interval that counts rows covers 53.42%. The same five unequal sizes laid out two ways give design effects of 9.3158 and 5.4652.

The two standardised means, and the shape of Fieller's set for their ratio at a = 3, d = 1. Each dot is one pair (zx, zy) drawn around (3, 1). Outside the horizontal band |zy| > 1.96 Fieller's set is a bounded interval, with probability 17.01%; inside the band and outside the disc of radius 1.96 it is everything outside an interval, 75.03%; inside the disc it is the whole line, 7.96%. On 40,000 counted draws Fieller covers ρ = 3.00 95.21% of the time and the delta interval 82.48%.

The distribution itself

A ratio whose interval has to be the whole line

The delta interval for a ratio of two means covers 95.61% when the denominator is eight standard errors from zero and 1.10% at a ten-thousandth of one, and ten times as wide it still covers only 3.48%. Linearising is not the fault. Gleser and Hwang proved that every interval that is always finite fails the same way, so an interval that keeps its promise has to be the whole line some of the time.

One treatment, a different hazard ratio at every follow-up. The hazard ratio a Cox model converges to, found as the root of its expected score by numerical integration, as the trial runs longer; dropout at 0.1 throughout. The proportional treatment reads 0.5 at every τ. The waning treatment reads 0.5000 at τ = 1, 0.6362 at τ = 3 and 0.7890 at τ = 8 — the same two arms, the same effect in the same first year, and a number that drifts towards one as later, effect-free events are added to the average. The dots are the mean of 400 Cox fits with 400 subjects an arm: 0.5014 at τ = 1, 0.7020 at τ = 2, 0.7635 at τ = 3, 0.8034 at τ = 5, 0.8208 at τ = 8. The crossing treatment reads 0.3429 at τ = 1, exactly 1 at τ = 3 by construction, and 1.0611 at τ = 8: beneficial, null or harmful according to when the trial stopped.

When the data stops early

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.

One row at x = 9 on a wrong line, fitted three ways. Least squares gives slope −0.389, Huber 0.171 with the extra row at weight 0.115, and least trimmed squares 0.420, fitted to the 12 rows it keeps. The twenty clean rows alone give 0.495. Open circles are the rows the trimmed fit leaves out.

Regression, and what the summary hides

A robust loss and a far x

One far row drags least squares to a slope of −0.389. Huber's loss, the standard robust line, reaches only 0.171, and carried further out the same row gets its full weight back. Least trimmed squares reads 0.420 at every distance, and at the normal model keeps 7.13% of least squares' efficiency to do it.

Reversals that are not errors

A lead that a heavy tail keeps

Four populations whose readings all correlate at exactly 0.6, and whose least-squares slopes all read 0.6. Select the top one per cent on one reading and measure them again: they keep 60% of their lead if the true scores are normal, 76.1% if they are Laplace, 78.4% if they are a t on four degrees of freedom — and 44.3% if they are uniform. The correlation predicts the regression of the extremes for one shape of population only.

Estimating P(Z > 5) = 2.8665×10⁻⁷ with plain draws and with four proposals. One seed each. Plain simulation draws nothing past 5 in 100,000 and estimates zero throughout. At 100,000 draws the proposal N(5, 1) reads 1.009 of the truth, N(9, 1) 1.041, N(4.5, 0.25²) 1.039 and N(5, 0.3²) 1.008. Values above 2.2 are drawn at the top edge.

What makes it checkable

The draws aimed at the tail

The chance a standard normal exceeds 5 is 2.8665×10⁻⁷, and a plain simulation needs 349 million draws to estimate it to within ten per cent. Draws aimed at the tail and weighted back need 565. Aimed slightly too narrowly, the same method has an infinite variance, an interval that covers 86.0% and gets worse with more draws, and an effective sample size that reads healthier than a proposal that works.

Three intervals as one strength is spread thinner, at a concentration of 8. Coverage of three nominal 95.0% intervals on the same 1000 draws of 200 rows at each count, when a total concentration parameter of 8 is spread over 1 to 32 instruments. Two-stage least squares covers 97.2%, 96.4%, 94.0%, 86.7%, 73.2%, 51.5%. Building each row's fitted treatment from a first stage that never saw that row covers 97.1%, 97.2%, 98.3%, 97.8%, 97.9%, 98.7%. Limited-information maximum likelihood with its conventional standard error covers 97.2%, 96.7%, 95.7%, 90.9%, 85.2%, 79.0%. At one instrument the likelihood estimator is two-stage least squares exactly, which is why the first readings of those two agree to the last draw.

A variable that moves one thing only

Leaving each row out of its own first stage

Spread a fixed first-stage strength over thirty-two instruments and two-stage least squares covers 51.5%. Build each row's fitted treatment from a first stage that never saw that row and the same draws cover 98.7% — through an interval 5.99 times as wide, around an estimate that misses by more than the whole effect on 34.7% of draws. At eight times the strength the same repair covers 95.3% and costs a width factor of 1.66.

One curve, and two forecasters that are each a single point. The ROC curve of an honest forecaster whose signal has correlation 1 with the latent state — every threshold on its probability, from the bivariate normal — and two forecasters that only ever say 0 or 1. The one an absolute-error score pays for says 1 wherever the honest probability exceeds a half: it has a true-positive rate of 0.6742 and a false-positive rate of 0.1375, and its "curve" is the two straight segments through that point, with area (TPR + TNR)/2 = 0.7684. The honest curve's area is 0.8683. Thresholding at the base rate of 0.3744 instead of at a half gives the largest area any two-valued forecaster can have here, 0.7818, and it is still 0.0866 short.

A forecast that is a probability

The liar with two answers

The forecaster an absolute-error score pays for says only 0 or 1, and on the ROC square it is a single point: its area is (TPR + TNR)/2 = 0.7684, against the honest forecaster's 0.8683, and it falls below the honest one on 200 of 200 counted records. No relabelling of its two answers returns what it threw away — the best recovers a Brier score short of the honest one by exactly the 0.022154 of resolution lost — and below a signal correlation of 0.7332 the same score prefers saying no every time to an honest forecast.

Weights that balance a sample by construction. What three sets of weights leave of the standardised difference between the arms on each covariate, as a root mean square over 1200 samples of 600 units. The true propensity leaves 0.1317 and 0.1186 — a sampling error, since it is right about the population and knows nothing of the draw. A likelihood fit leaves 0.0770 and 0.0657, having absorbed part of the draw's imbalance as a side effect of fitting the treatment. Weights fitted so that each arm's weighted means are the sample's leave 1.4e-14 and 1.2e-14, which is the arithmetic's floor rather than a small number: the largest gap between a weighted arm mean and the sample mean in any draw is 9.8e-14.

Weighting one sample into another

A weight fitted to balance

Weights fitted so that each arm's weighted covariate means equal the sample's leave a difference of 1.4×10⁻¹⁴ between the arms and give the estimate a third of the variance of weights fitted by likelihood — 0.011883, within a relative 5.8% of the bound no estimator can beat. In the world where the assignment carries a square nobody named, the same exact balance leaves the square further apart than no weighting at all, and where the outcome carries it too the estimate is wrong by 0.6973 with an interval that covers 1.5%.

Three ways to reject with two studies, drawn where the two z statistics live. Two one-sided studies, each summarised by its z statistic. Fisher's combination rejects outside a curve that runs parallel to both axes, so one study past z = 2.378 decides it alone; Stouffer's rejects above the straight line z₁ + z₂ = 2.326; Tippett's rejects when either z passes 1.955. Each region holds exactly 5% of the standard bivariate normal — Fisher's in closed form, e^(−c/2)(1 + c/2) at c = 9.488 — and of 100,000 counted null pairs they catch 4.95%, 4.88% and 5.04%. Two alternatives carry the same Stouffer evidence: one study at 2.326 and the other at nothing, where the powers are 62.7%, 50.0% and 65.4%; and both at 1.163, where they are 47.7%, 50.0% and 38.3%.

Tests, and the second number

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.

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.

Stopping rules

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%.

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%.

Corrections, and what each controls

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 Box–Behnken design in three factors: 15 runs, none at a corner. Twelve runs at the midpoints of the cube's edges and 3 at its centre. Every run holds one factor at zero, so no run puts all three factors at an extreme — which is what makes it runnable where a corner is not. The three panels are the design's coordinate projections, with repeated positions marked.

Decided before the data

The design that refuses the corners

Box–Behnken runs three factors in fifteen runs and puts none of them at a corner, which is what makes it usable where a corner cannot be run. It predicts the corner 1.84 times worse than the seventeen-run design that goes there, and 1.31 times worse at the middle of a face, and all three numbers are matrix computations with no simulation in them.

A design chosen rather than looked up

Augmenting a design that has already run

The equivalence theorem still certifies when some runs are already spent, and one number in it changes: the bound is no longer p but (p − λ·tr(M⁻¹M_fixed))/(1 − λ). It equals p again exactly when the runs already made can still be absorbed into the design that would have been chosen — so the certificate says whether the experiment is still recoverable.

The ridge, when the fitted optimum is outside the region. One fitted surface. Its stationary point is at a radius of 2.289 and the fit calls the shape a maximum. The ridge is the best setting at each radius, found by the Lagrange condition (B̂ − μI)x = −ĝ/2; the fitted response rises along it from 59.93 at the centre to 62.10 at the edge. The true optimum is at (0.4, 0.3).

The surface between the corners

When the best setting is outside the region

On a flat surface at twice the noise the fitted optimum lands outside the experimental region on 24.9% of studies and more than three coded units out on 11.8%. The answer is a ridge — the best setting at each radius, with a closed form — and the two obvious rules for using it turn out to be within four per cent of each other.

Four 95% intervals for the odds after 2 of 20. credible, transformed: 0.0218 to 0.3964. Wald, transformed: -0.0305 to 0.3012. delta method on the odds: -0.0512 to 0.2734. delta method on the log-odds: 0.0258 to 0.4789. The first two are the same intervals for the proportion with their endpoints put through the odds; the last two are fresh approximations made on the new scale.

The prior, doing visible work

An interval for something else

An interval for the odds is free — put the endpoints through the odds and the coverage does not move, exactly, for any interval at all. The method everyone uses instead computes a new standard error on the new scale, and at twenty trials that costs four points of coverage, produces negative odds, and has no value at all when nothing was observed.

Too small breaks it and too large does not. Coverage of the weighted interval against the factor the true likelihood ratio is multiplied by, at a test population 80.0% drawn from the noisier group and 200 calibration points. The exact weight is the factor of 1 and covers 95.70%. Overstating it costs nothing: 96.13% at sixteen times too large. Understating it costs, and costs steeply below about a half — 94.93% at half, 88.37% at an eighth and 67.90% at a thirtieth. The question this answers was whether a wrong weight degrades smoothly or falls off a cliff, and the answer is that it does neither symmetrically: the curve is smooth and one-sided.

Coverage without a distribution

The weight that has to be estimated

A likelihood ratio sixteen times too large costs 5.5% of interval width and no coverage at all; one a thirtieth of the right size covers 67.90%. The estimate from a batch of five unlabelled covariates covers 95.10% against an exact repair's 95.30%, and the binomial says why.

One statistic that is right under both hypotheses. Rejection rates for both statistics under both nulls, at 25% of 150 units treated, with the weak-null readings taken at an effect spread of 3. The difference in means is exact under the sharp null and rejects 22.93% of true weak nulls. The studentised difference is exact under the sharp null — 4.07% — and reads 6.27% under the weak one. The repair is a change of statistic inside the same construction: the same re-randomisations, the same fixed outcomes, a different number compared across them.

The reference distribution the design supplies

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.

What a corrected critical value delivers to a t statistic: actual size over nominal, upper tail, 30 exponential draws. At a nominal 1% the upper-tail t test's actual size is ×0.153 with Student's quantile, ×2.94 with one Cornish–Fisher term and ×1.51 with Hall's cubic, both using the source's skewness, and ×0.878 with Hall's cubic using each sample's own. At 10⁻⁶ they are under a hundredth of nominal, ×1.04e+4, ×50.0 and ×1.59.

Past the first term of the normal approximation

The correction a t test would use

On thirty exponential draws the one skewness term that held a sum's critical value within 10% out to five standard deviations nearly triples a t test's 1% size when the source's skewness is known, and its upper critical value turns back — at a level of 0.89% on ten draws, where a test asked for one in a thousand rejects 121 times too often. Hall's monotone cubic removes the turn and gains a floor. Built from the sample's own skewness it holds the short side within 20% from 10% down to one in a hundred thousand, and leaves the long side, the one a safety limit reads, at twice its level: the samples that fail are the ones that hide their skewness.

What two exact companions are worth to a simulated rate: the lognormal t test's size post-stratified three ways, by the number of cells. To first order, bands of the logarithms' t statistic are worth at most 2.77 times the draws; a 32 × 32 grid in the pair 4.68; bands of a score fitted to the pair on a thousand samples 4.64 at sixteen bands and 4.69 at sixty-four. Counted over runs of 4,000 samples, the grid of 1,024 cells was worth 1.97, with 94 cells a run left empty.

A cut point, at a correlation

A companion with two coordinates

The logarithms' t statistic, cut into bands, is worth at most 2.77 times the draws to a simulation of the lognormal t test's size. It is one function of two exactly known statistics, the logarithms' mean and spread, and the pair is worth 4.64 when a score fitted to it on a pilot of a thousand samples is cut into sixteen bands whose probabilities are integrated exactly. A grid of cells in the pair needs a thousand cells to reach the same and, counted on runs of four thousand samples, is worth 1.97. Band weights estimated from a pilot instead of computed are worth less than the pilot's draws would have been had they simply been counted — exactly nothing at a pilot the size of the run.

Seven products of three splits. The correlation of every product of three centred median splits with every other, at a Spearman rank correlation of 0.4 between each pair of covariates. Under a Gaussian copula a main effect correlates with the other mains and with the triple (0.273), and with no pair at all, because the third moment is 0.000. Under a Frank copula, whose pairs are radially symmetric, the third moment is 0.078 and every other cell fills in: a main correlates 0.082 with the pair it is not in. In both panels a main is exactly uncorrelated with a pair it belongs to, which is the known zero.

Both halves of the dependence at once

The zero that needed two

A rule balancing two median splits removes nothing of their interaction, on every copula, because a centred split squares to a constant. Add a third covariate and the same arithmetic stops protecting the thing it looked as if it protected. The product of three splits is not orthogonal to the mains: at a rank correlation of 0.4 a rule on the mains removes 14.47% of it under a Gaussian copula. And the symmetry that decides the rest belongs to the triple rather than the pair, so Frank's copula, whose pairs are radially symmetric, leaks where Clayton's, whose pairs are not, barely does.

The same table at seven correlations

A cut on each side

Every table of the threshold's leak put one quantile on both covariates, which is the diagonal of a surface nobody had drawn. Off the diagonal the copulas swap places: a cut at the 5th percentile on one covariate and the 95th on the other removes 54.8% of the interaction under a Gaussian copula and 1.1% under a t copula, the reverse of their order at the near corner. Walked further out, the far corner has two opposite limits, and which one a Gaussian reaches is decided by whether its correlation is above or below exactly one third.

Three charges and two counts. The optimism of an in-sample fit of the widest candidate on 120 rows, in units of its own error variance, over 1500 draws, by persistence. Counted on the 40 rows straight after the sample: 11.1, 21.5, 35.6, 51.5, 65.5, 87.8, 119.1. Counted on rows 600 further on: 9.3, 18.3, 33.0, 50.6, 67.0, 96.1, 159.0. Charged by the long-series inflation: 10.0, 19.3, 34.7, 54.4, 74.3, 114.2, 234.1. Charged by the same inflation summed over the sample's rows: 10.0, 19.2, 34.2, 53.1, 71.8, 108.2, 208.8. Charged by twice the trace of the hat matrix against the errors' correlation on the sample's own design: 10.0, 18.7, 32.0, 47.5, 61.5, 85.2, 132.2.

Scoring a search without spending data

A charge the sample can afford

The inflation charge for dependent rows runs to twice the counted optimism at persistence 0.95, and the reason offered was that a series of n rows cannot be optimistic about movements slower than n rows. Summing the inflation over n rows does almost nothing: 234 becomes 209, against 119 counted. Evaluating the same variance on the sample's own design gives 132, and moving the fresh rows away from the sample raises the count to 159. So the charge can be made nearly right, and when it is, the regret doubles from 0.032 to 0.061. A selection wants a much larger charge than the optimism, and past about fifty per predictor it is no longer selecting.

$Three repairs at one requirement. Coverage against spend at a half-width of 0.4 and a first stage of 5, all exact. A floor on the second stage at 5, 8, 10, 12, 15, 18, 21, 24 observations covers 88.4%, 91.4%, 92.4%, 93.1%, 93.9%, 94.6%, 95.3%, 96.0% at 0.86, 0.94, 0.97, 1.00, 1.02, 1.05, 1.09, 1.14 times the oracle's spend. The second stage reading with t, with its fraction dialled from 0.2 to 1, covers 88.1%, 89.0%, 90.6%, 92.1%, 93.4%, 94.4%, 95.2%, 95.9%, 96.4% at 0.84, 0.91, 1.02, 1.17, 1.34, 1.52, 1.70, 1.89, 2.08 times. A constant at the end covers 88.4%, 89.4%, 90.4%, 91.3%, 92.1%, 92.9%, 93.6%, 94.2%, 95.0%, 95.7% at 0.86, 0.90, 0.94, 0.98, 1.02, 1.06, 1.10, 1.14, 1.20, 1.26 times.$ What the design is asked to guarantee

A floor that reads the first stage

A three-stage stopping rule fails at a first stage of five because a low first reading asks for nothing more, and the only floors that repair it were set near the answer, by somebody who already knew roughly what the spread was. Inflating the first reading by Stein's own factor needs no such knowledge, and it does cut the experiments left stuck from a fifth to a fifteenth. But those still stuck cover less than before, the rule needs a different dial at every requirement, and a floor of 26 observations covers 96.5% at the spend where the rule covers 92.1%, even met by a spread it was not set for.

Balancing what has no levels

A second reading or a second covariate

A rule that balances a recording balances the truth only as far as the recording reaches, and a second reading of the covariate raises that reach. So does a first reading of something else. At a reliability of 0.8 the first reading of a second covariate does more once that covariate matters a third as much as the first, and the threshold is exact: the square root of (1 − λ)/(1 + λ), with no trial size in it. A protocol's list of measurements turns out to be a small knapsack, and it is rarely filled by reading anything twice.

What the interval covers as the effect stops being one number. Coverage at 120 units under minimisation, 600 trials and 199 re-run allocations each, as the effect's slope on the prognosis rises from 0 to 1.5. the inverted test, unadjusted, for the population's mean: 96.7%, 96.2%, 95.7%, 95.7%, 94.8%. the same, for the sample's mean: 96.7%, 96.0%, 96.2%, 97.3%, 98.3%. the inverted test, adjusted, for the population's mean: 96.5%, 95.5%, 95.0%, 95.3%, 96.0%. the same, for the sample's mean: 96.5%, 95.7%, 96.5%, 98.0%, 99.5%. the regression with an interaction, for the population's mean: 96.2%, 95.5%, 94.0%, 91.0%, 84.0%. the same, for the sample's mean: 96.2%, 95.8%, 96.2%, 95.7%, 95.2%.

Balancing on what was recorded first

An effect that is not one number

A randomisation test becomes an interval for the effect by testing every constant effect in turn, so when the effect grows with the prognosis every hypothesis it tests is false. It does not fall apart. It covers the population's mean effect within a point of its level at every slope measured, and its width grows by exactly what the sample's own composition adds. A regression that models the interaction stays narrow at 0.72, covers the sample's mean at 95%, and covers the population's at 84%. The extra width was never a defect. It was the difference between two questions.

When the set is too large to walk

A floor for the draw

A basis drawn at random guarantees more on average than any fixed one, at the price of leaving some shape wholly untouched in a large share of trials. Requiring every basis in the draw to keep a floor looks like a smooth trade between the two. It is a staircase, and the first step does nearly all the work. No basis has a floor between zero and 31.83%, so there is nothing to give up until a floor of that size is asked for. And at four functions, seven bases tie at the fixed basis's own 63.66%: a mixture of them keeps that floor exactly and adds thirteen points to the guarantee.

Choosing what the rule reads

A box with a count

The ellipse never runs out of assignments and holds the named functions loosely; the box holds them tightly and can come up empty. Dropping the ellipse's thin directions was meant to give both, and it does not: no cutoff comes within a third of the box. But the box's emptiness was never a property of the box. It belongs to a tolerance fixed in advance. Set the tolerance by a count instead, and at that count the region is the box, on every set of units, with nothing left to run out.

A guarantee that needed a symmetry

The covariate on its ranks

A skewed covariate spoils every parity argument a balancing rule relies on, and a rule that balances ranks instead of values looks like the way out, since a rank has the same uniform law on any marginal. The measurement says the skew really does belong to the scale for one kind of shape: a rank holds a median split at exactly a quarter of a coin's imbalance whatever the covariate. But it pays with a cap on any shape linear in the value, at nearly half a coin's imbalance on the strongest skew. And a rule holding values and median splits together holds both, beating the rank on the shape a rank gives up and matching it on the one it gains.

The excess over the Gaussian displacement, by window. By how much the expected leverage per parameter exceeds the Gaussian closed form, with the fresh row integrated out, at windows 20, 40, 80, 160, 320, 640. normal: -0.90%, -0.61%, -0.04%, -0.06%, -0.02%, 0.00%. t on eight: 4.14%, 2.78%, 1.79%, 0.73%, 0.28%, 0.18%. t on five: 10.70%, 7.50%, 3.93%, 2.01%, 1.26%, 0.70%. t on three: 44.44%, 32.67%, 22.62%, 16.43%, 11.70%, 7.63%. exponential: 27.91%, 14.01%, 7.21%, 3.53%, 1.93%, 0.85%. On normal predictors the closed form is exact from a window of 80.

A search with no fixed point

An excess and its window

The parameter-count displacement is a Gaussian fact, and on heavy-tailed predictors it runs a few per cent over. Swept across windows from 20 to 640 rows, the excess is about the predictors' excess kurtosis divided by the window: a law with a fourth moment of nine on 80 rows is 7.5% over, and on 640 rows under one. At three degrees of freedom it falls only as the root of the window, from 44% to 7.6%. And the instability once blamed on that law was not there: with the fresh row integrated out, the batches agree to a point and a half, and the mean exists.

A block, weighted inside itself

A sequence that knows it was centred

A block length read off a sample's own autocovariances gets worse the further out it reads, because a centred series' autocovariances sum to exactly zero. To first order every lag loses the same amount, about the long-run variance over the sample size, and that can be added back. Corrected, a reading to lag forty goes from 84.5% to 89.2%, and to lag twelve from 93.3% to 94.5%. But the correction overshoots on the long lags, and on the rule that picks its own cut-off, which is short, it moves coverage by three tenths of a point. The identity was the reason the lag mattered. It was not the reason the rule falls short.

How often each combination, and each union of them, rejects ten studies of nothing. Each combination alone rejects exactly 5% of null sets. Counted on 1,000,000 sets of ten null studies: Fisher or Stouffer 6.63%, Fisher or Tippett 8.05%, Stouffer or Tippett 8.96%, any of the three 9.66% — enclosed on a two-dimensional lattice between 9.18% and 10.09% — and all three together 1.05%. The three sizes add to 15%.

Tests, and the second number

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.

The honest curve, and the same forecaster in three coarse vocabularies. The ROC curve of the honest probability at full signal, area 0.8683, beside the same forecaster rounded to the nearest whole number, area 0.7684 — the two-valued liar — to the nearest half, area 0.8205, and to the nearest tenth, area 0.8650. A vocabulary of v values is v points on the square joined by straight segments, and tied reports count half.

A forecast that is a probability

A forecaster that rounds

An honest probability issued in tenths loses 0.0033 of ROC area and 0.000708 of resolution — the variance its bands average away, and 89.5% of the 0.000792 it adds to the Brier score. Two hundred records of two thousand forecasts show that loss on 189; it takes about 3,300 forecasts to put it two standard errors from zero. And 3.207 in every thousand forecasts in tenths are a 0% on an event that happened, which a logarithmic score charges without limit.

The difference in restricted mean survival at every horizon, in three worlds. Treatment minus control, in closed form, with dropout irrelevant to the truth. The proportional treatment's difference grows to 0.4766 at τ = 3 and the waning treatment's to 0.2675. The crossing treatment's rises to 0.1776 at τ = 2, near where the two survival curves cross, and falls back to 0.1366 at τ = 3. The ticks along the bottom are the eleven horizons, from 0.5 to 3 in quarters, at which a trial below reads its differences.

When the data stops early

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.

Regression, and what the summary hides

The start an efficient robust line inherits

The MM-estimator carries a trimmed fit on through a redescending loss, and it does what it promises on one far row: slope 0.479 at every distance, the row at weight exactly zero, and 87.2% of least squares' efficiency at twenty rows. What it cannot do is choose. At eight far rows of twenty the exact trimmed fit picks the wrong half on 111 datasets; the efficient step repairs none of them, spoils none of the other 89, and ends nearer the wrong line than the start did.

Three intervals as one strength is spread thinner, at a concentration of 8. Coverage of four nominal 95.0% intervals on the same 1000 draws of 200 rows at each count, when a total concentration parameter of 8 is spread over 1 to 32 instruments. Two-stage least squares covers 97.2%, 96.4%, 94.0%, 86.7%, 73.2%, 51.5%. Building each row's fitted treatment from a first stage that never saw that row covers 97.1%, 97.2%, 98.3%, 97.8%, 97.9%, 98.7%. Limited-information maximum likelihood with its conventional standard error covers 97.2%, 96.7%, 95.7%, 90.9%, 85.2%, 79.0%. The same estimate with Bekker's many-instrument standard error covers 97.2%, 97.2%, 97.2%, 95.0%, 94.3%, 93.8%. At one instrument the likelihood estimator is two-stage least squares exactly, which is why the first readings of those two agree to the last draw.

A variable that moves one thing only

A standard error that knows about the instruments

Limited-information maximum likelihood came out least biased when a concentration parameter of 8 was spread over thirty-two instruments, and its conventional interval covered 79.0%. Bekker's many-instrument standard error covers 93.8% on the same draws, at 63% of the jackknife's width — and it gets there with a median standard error of 0.561 against a true spread of 0.797, because it is large on the draws that need it. At eight times the strength it covers 94.9% at 91% of the jackknife's width, and nothing measured here beats it.

One weighting told the means and one told the second moments, in five worlds. The bias of the fit to balance over 600 samples of 600 units in each world, fitted to the covariates' means and fitted to their means, squares and product. Told the means it is off by -0.0004, -0.0020, 0.0103, 0.6973, 0.2698 in the worlds with no square, a square in the assignment, a square in the outcome, a square in both and a cube in both; told the second moments, by -0.0009, -0.0000, 0.0009, -0.0045, 0.3099. Its interval covers 94.0%, 94.7%, 95.0%, 1.5%, 51.0% and 93.7%, 89.8%, 94.0%, 91.0%, 48.3%.

Weighting one sample into another

The moments a balance is told

Weights fitted to balance the covariates' means were wrong by 0.6973 in the world where both the assignment and the outcome carry a square. Told the squares and the product as well, the same construction is off by −0.0045 there and its interval covers 91.0%. The failure moves up a moment rather than away: with a cube in both, the second-moment balance is off by 0.3099 and leaves the cube twice as far apart as no weighting. And where overlap is thin, 37.0% of samples have no such weights at all.

Reversals that are not errors

The slope of a density nobody can see

Tweedie's formula corrects a reading by the slope of the readings' own log-density, and a study has its readings. Estimated from a thousand of them, the correction for the top one per cent beats the correlation's linear rule on 84.0% to 98.0% of studies from heavy-tailed populations and on 75.0% to 81.5% from a bounded one — and costs an error of 0.09 to 0.12 where the population is normal and the rule was already exact. At 250 readings the log-spline loses to the rule it replaces, and at 16,000 the same log-spline gets worse on a power tail.

A run length of 4 makes every exceedance its own cluster. 200 steps of a max-moving-maximum, X(t) = max(0.4·Z(t), 0.3·Z(t−6), 0.3·Z(t−12)) with unit Fréchet innovations Z, whose extremal index is exactly 0.40: one large innovation can put three readings above a threshold, 6 steps apart. The rule marks the 0.9 quantile and 19 readings clear it; 12 of the gaps between consecutive exceedances are exactly 6 steps. With a run length of 4, so that two exceedances 4 or more steps apart start separate clusters, they form 19 clusters, shaded, the largest holding 1. The runs estimator reads 1.000 against 0.40.

The tail past the last observation

The run length a declustering chooses

The runs estimator of an extremal index carries a constant nobody derives. Where a cluster is a run of neighbouring exceedances the constant barely matters; where a cluster's members fall six steps apart, the estimate is 0.9069 at a run length of six and 0.3649 at seven against an index of 0.40, and a run length of four removes under a tenth of the overstatement declustering exists to remove. A rule that reads the run length off the data has the smallest worst error of the three.

The value that is not there

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.

What one lost run costs a 16-run factorial fitting 11 coefficients. Every run is worth the same: dropping any one multiplies every coefficient's variance by 1.2000, which is 1 + 1/(N − p) with N = 16 and p = 11, and gives every pair of coefficients a correlation of 0.1667 where the complete design had exactly zero.

Decided before the data

The run that did not happen

Lose one run from any orthogonal design and every coefficient's variance is multiplied by exactly 1 + 1/(N − p), and every pair of coefficients acquires a correlation of exactly 1/(N − p + 1) where there was none. The price is set by the design's spare capacity and by nothing else, and a saturated design cannot survive it at all.

Where each criterion's optimum puts the information. the D-optimal design's smallest eigenvalue is 0.09927, attained once; the A-optimal design's smallest eigenvalue is 0.16516, attained once; the I-optimal design's smallest eigenvalue is 0.17541, attained once; the E-optimal design's smallest eigenvalue is 0.19999, attained 2 times. A criterion that reads the smallest eigenvalue has no derivative where that eigenvalue is repeated, and the E-optimal design is exactly there.

A design chosen rather than looked up

The criterion with no derivative

E-optimality maximises the smallest eigenvalue of the information matrix, and at its own optimum that eigenvalue is attained twice — which is exactly where the function has a corner. The multiplicative search this field's other three criteria use assumes a derivative that is not there, and stops at 37.2% of the optimum.

Two companions on one simulation, two hundredfold apart. How many times as many draws each companion is worth, on the same 4,000 simulated samples of 40 observations. The coverage of the interval is estimated with the observed count as its companion, whose expectation is 12 exactly; they correlate at 0.2665 and the companion is worth 1.08 times the draws. The expected width is estimated with p̂(1 − p̂) as its companion, whose expectation is 0.20475 exactly; they correlate at 0.9977 because the width is a monotone function of it, and the companion is worth 214 times the draws — 856 thousand simulated samples' worth of precision from four thousand.

What makes it checkable

The check worth more than the check

The same exactly known companion that verifies a simulation can sharpen it. On one set of four thousand draws, one companion is worth 1.08 times the draws and another is worth 214 times them, and the factor is 1 − ρ² with nothing else in it.

The law is the eigenvalues, and nothing else. The mean and the skewness of n(ĝ − g) at the stationary point, measured over 40,000 draws, against the closed forms: half the sum of the Hessian's eigenvalues for the mean, and for the skewness twice root two times the sum of their cubes over the sum of their squares to the power three halves. The worst disagreement anywhere is 0.028. In one variable the second-order law is a single chi-square with one degree of freedom and its sign is the sign of the second derivative; here it is a weighted sum with the Hessian's eigenvalues as weights, so a bowl and a valley differ in both moments and a saddle has both equal to zero.

The distribution itself

A flat point with more than one direction

At a stationary point of a function of several means the second-order law is ½ Z′HZ, so the bias is half the Hessian's trace — 2.008 for a bowl, 5.028 for a valley, and −0.006 for a saddle, where the eigenvalues cancel. The saddle's coverage is the worst of the three.

Stopping rules

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.

How often four permutation tests of a covariate-adjusted effect reject a true weak null, effect varying with the outcome, 25% of 150 treated. At an effect spread of 0, 0.5, 1, 1.5, 2: the adjusted coefficient's permutation test rejects 5.9%, 10.8%, 13.2%, 16.6%, 14.8%; over its sandwich standard error, 5.7%, 5.0%, 3.4%, 3.4%, 3.0%; the coefficient with a treatment-by-covariate interaction, 5.1%, 10.2%, 12.8%, 14.7%, 14.0%; the same over its sandwich standard error, 5.7%, 5.2%, 5.2%, 5.1%, 3.9%.

The reference distribution the design supplies

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%.

Past the first term of the normal approximation

A tilt for the ratio

A t statistic is a function of two means, so its saddlepoint tilts the joint law of each draw and its square. On an exponential source every such tilt is a truncated normal, and none has a coefficient of variation above one — the exponential is the edge of its own family. Integrated over the samples a tilt can reach, the saddlepoint reads a t statistic's tails on thirty draws within 2.5% from 10% to one in a million on the long side, with nothing fitted. The samples it cannot reach are a third of all samples, they sit at the centre of the statistic rather than in its tails, and a larger sample has more of them.

Approximate weights against the size of the run. What sixteen bands of the logarithms' t statistic are worth to a simulation of the lognormal t test's lower-tail size, in multiples of the draws, against the size of the run, with the band weights from Student's t exactly and from three approximations to it. Exact weights are worth 2.709 at every size. Fisher's one-term expansion is worth 2.708 at four thousand draws and 2.523 at a million, and breaks even with counting at 23.7 million draws. The variance-matched normal is worth 1.849 at four thousand and breaks even at 14,698. The standard normal is worth 0.762 at a thousand and breaks even at 669: a bias that does not shrink is multiplied by every draw added.

A cut point, at a correlation

Weights from an approximate law

A companion whose law is only approximately known can still be cut into bands, with each band's weight computed from the approximation. The weight's error is a bias that does not shrink, and the run multiplies it: the stratified rate is worth p(1 − p)/(v + Nb²) times the draws. Reading Student's t on nineteen degrees of freedom as normal breaks even at 669 draws; the normal with the t's variance at about fifteen thousand; Fisher's one-term expansion at twenty-four million. What decides the bias is how the weight errors line up with the band rates, not how large they are — Fisher's is wrong by sixty per cent in one band and biases the rate by six hundredths of one.

Stopping rules

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.

The E-optimality certificate along the axis x₂ = 0. The certificate — a fifth of the squared distance of the point's squared radius from one, plus a fifth of the squared difference of its two squared coordinates — along the axis x₂ = 0, with its two pieces drawn alone at full weight: the radial piece, a third of the squared distance from the unit circle in squared radius, which reaches 0.333 here, and the cross piece, half the squared difference of the squared coordinates, which reaches 0.500. The certificate's largest value on the cut is 0.2000, reached at x = -1.0, 0.0, 1.0; the smallest eigenvalue of the nine-point design is 0.2.

A design chosen rather than looked up

A certificate for the worst direction

E-optimality was the one design criterion here whose answer was claimed rather than proved. It has a certificate after all, and on the square it fits on one line — (1⁄5)(1 − x₁² − x₂²)² + (1⁄5)(x₁² − x₂²)², which never exceeds 1⁄5 and touches it at exactly the nine points of the 3² grid. That proves the design with 2⁄5 of its weight at the centre, 1⁄10 at each edge midpoint and 1⁄20 at each corner is E-optimal on the whole square, and it is built from two directions mixed three to two, either of which alone fails.

Ten studies every study shares the control: the three combinations read as though independent, by the correlation. Counted on 400,000 null sets of ten one-sided studies at each correlation, every study shares the control. Fisher: 5.00%, 9.54%, 12.83%, 15.01%, 16.63%, 17.88%, 18.80%. Stouffer: 5.00%, 11.51%, 16.29%, 19.54%, 22.20%, 24.23%, 25.86%. Tippett: 4.98%, 4.86%, 4.68%, 4.45%, 4.17%, 3.72%, 3.27%. Smallest of three: 9.66%, 14.44%, 17.94%, 20.41%, 22.55%, 24.34%, 25.88% — at correlations 0, 0.1, 0.2, 0.3, 0.4, 0.5, 0.6. Each combination is read at its critical value for independent studies.

Tests, and the second number

Studies that share a control

Ten comparisons against one control arm of the same size are correlated at exactly one half, and combined as though they were independent, Stouffer's sum rejects 24.23% of sets in which nothing works, Fisher's 17.88%, while Tippett's smallest p-value falls to 3.72%. Repaired with the correlation the design states, each is exact again — and the smallest of the three is then inflated less than for independent studies, 7.05% against 9.66%, because sharing makes the three combinations agree. The two inflations the dependence was expected to stack do not stack.

Where three vocabularies of 5 values put their cuts, under the honest forecasts they divide. The density of the honest probability at full signal, piled toward small values because the event happens 37.4% of the time, and below it three ways of cutting it into 5 groups, each printing its group's event rate. 5 equal-width bins: cuts at 0.200, 0.400, 0.600, 0.800, printed values 0.075, 0.295, 0.497, 0.698, 0.904, resolution lost 0.003454. 5 equal-mass groups: cuts at 0.066, 0.211, 0.422, 0.695, printed values 0.025, 0.132, 0.311, 0.554, 0.850, resolution lost 0.004046. the best 5: cuts at 0.145, 0.339, 0.552, 0.777, printed values 0.054, 0.236, 0.441, 0.662, 0.892, resolution lost 0.003193. The density is cut off at 3.2 near zero, where it grows without bound. The best vocabulary's cuts sit halfway between neighbouring printed values, and its printed values sit at their groups' event rates; no other partition into 5 groups loses less.

A forecast that is a probability

Five values chosen by the forecasts

The vocabulary of five calibrated values that loses least on the Brier score puts its cuts at 0.145, 0.339, 0.552 and 0.777, and gives up 0.003193 of resolution against 0.003454 for equal-width bins and 0.004046 for equal-mass groups. Eleven such values beat tenths by 18.5% — but only once someone knows where to cut. Fitted on a record of two thousand forecasts the same eleven add 0.001547, about twice what tenths add with nothing fitted, and they draw level only near twelve thousand. For users acting at chances near one in ten, a vocabulary cut for them lowers their regret by a factor of 7.5 and costs the Brier score nearly nine times as much.

Power of four tests of two survival curves, in three shapes of treatment effect, at 50, 100 and 200 a side. 6,000 trials at each setting, dropout 0.1 a year, follow-up to three years. hazard halved throughout, 50 a side: log-rank 64.9%, best of eleven horizons 51.7%, restricted mean at 3 61.1%, one test for all twelve 56.6%; hazard halved throughout, 100 a side: log-rank 91.8%, best of eleven horizons 81.0%, restricted mean at 3 88.4%, one test for all twelve 86.0%; hazard halved throughout, 200 a side: log-rank 99.7%, best of eleven horizons 98.4%, restricted mean at 3 99.4%, one test for all twelve 99.3%; halved for a year, then nothing, 50 a side: log-rank 18.5%, best of eleven horizons 32.1%, restricted mean at 3 26.6%, one test for all twelve 30.8%; halved for a year, then nothing, 100 a side: log-rank 29.3%, best of eleven horizons 51.7%, restricted mean at 3 42.5%, one test for all twelve 50.2%; halved for a year, then nothing, 200 a side: log-rank 51.4%, best of eleven horizons 81.4%, restricted mean at 3 70.3%, one test for all twelve 80.2%; curves that cross, 50 a side: log-rank 5.1%, best of eleven horizons 45.7%, restricted mean at 3 10.4%, one test for all twelve 44.0%; curves that cross, 100 a side: log-rank 5.2%, best of eleven horizons 76.7%, restricted mean at 3 16.4%, one test for all twelve 75.5%; curves that cross, 200 a side: log-rank 5.2%, best of eleven horizons 96.7%, restricted mean at 3 26.5%, one test for all twelve 96.6%.

When the data stops early

One test for a curve that might cross

The log-rank statistic and the differences in restricted mean survival at eleven horizons are one Gaussian vector under no effect, and its correlations are closed — from −0.461 at half a year to −0.949 at three, where the log-rank statistic is nearly the restricted mean itself. So one critical value, 2.374, prices the largest of all twelve. At 100 a side it keeps 93.6% of the log-rank test's power when the hazard is halved throughout and 98.5% of the best horizon's when the curves cross, where the log-rank test has none. Running both tests and keeping either rejection rejects 8.67% of trials with no effect.

Sixteen groups from two clusters: the true effects, the observed means and the pooled estimates, with the kurtosis of each. One dataset of 16 groups of four observations each, effects drawn from two clusters with total spread 2, noise 3. The fitted spread is 1.701, so every estimate is pulled 43.7% of the way to the centre -0.213. Kurtosis: true effects 1.203, observed means 2.348, pooled estimates 2.348 — the last two identical, because one is an affine image of the other.

Groups that borrow

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.

Five 95% intervals for an AR(1) forecast 6 steps ahead at φ = 0.85, fifty observations. Coverage on 4,000 series, the same series for every interval, each simulated interval built from 499 simulated futures. The plug-in formula: 88.48%. The formula, all three repairs: 92.80%. Simulated: parameters drawn: 92.55%. Simulated: residual bootstrap: 88.25%. Simulated: bootstrap, bias removed: 93.47%.

Comparing two forecasters

An interval built from simulated futures

A forecast interval read off simulated futures needs no delta method and no normal multiplier, and was expected to close the residual the three repairs to the formula leave. It does not close it on its own: the plain residual bootstrap covers 88.25% six steps ahead at φ = 0.85, the plug-in formula's 88.48% to within the count, because it simulates around the same biased persistence. With that bias removed inside the bootstrap it covers 93.47%, the best of five intervals, and its shortfall stops growing with the horizon — 93.80% at twelve steps, where the repaired formula covers 91.85%.

Testing for flatness at 5% before choosing the interval for a squared mean. Coverage of four nominal 95% intervals for μ², exact, against the true mean's distance δ from the flat point in standard errors. The tangent interval Z² ± 2z|Z| has its worst, 85.98%, at δ = 1.45. The second-order interval read off χ²₁ is right only at δ = 0 and falls to 34.22% at δ = 2. The two-stage rule, which uses the second-order interval when a 5% test does not reject flatness, has its worst, 49.72%, at δ = 1.96. The squared exact interval never falls below 95%.

The distribution itself

Testing for a flat point first

Test whether the gradient is zero, and if the test does not reject, read the interval off the second-order law that holds at a stationary point. For a squared mean that two-stage rule covers about 50% at its worst whatever the pretest's level — 49.72% with a 5% test, where the tangent interval it was meant to rescue never falls below 85.98% — because its worst sits exactly where the true distance equals the test's critical value, half the samples are declared flat there, and the second-order interval cannot reach the truth from any of them.

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