Past exam of the mathematics course of the University of Cambridge / 2013 / iii / Paper 35 (Design of Experiments)

Write $n=bk$, let $I_n$ be the identity matrix, let $J_m$ be the $m$-by-$m$ all-ones matrix, and put $B=\mathrm{diag}(J_k,\dots ,J_k)$, with one diagonal block per experimental block. The variance-covariance matrix isIts orthogonal decomposition is obtained by first subtracting each block's sample mean, then subtracting the grand sample mean from the block means. More explicitly, writing $x_{jt}$ for coordinate $t$ in block $j$, the three invariant subspaces areThey are pairwise orthogonal, with dimensions $b(k-1)$, $b-1$ and $1$, and their direct sum is ${\mathbb{R}}^n$. On $W$, both $B$ and $J_n$ vanish. On $U$, $B=kI$ and $J_n=0$. On $G$, $B=kI$ and $J_n=nI$. Thus the eigenvalues and corresponding invariant subspaces areIf some eigenvalues coincide, their eigenspace is the direct sum of the listed subspaces with that value. Zero-dimensional rows are omitted when $b=1$ or $k=1$. For an admissible covariance matrix the eigenvalues on nonzero subspaces must be nonnegative; these conditions are also sufficient for positive semidefiniteness. The expectation parameters do not affect this calculation.

An orthogonal block design has treatment contrasts orthogonal to block contrasts after removing the grand mean. This is a statement about vectors on the experimental units, with the usual inner product; the two full spaces are not orthogonal because both contain the constant vector.

For a counting criterion, let $n_{ij}$ count experimental units receiving treatment $i$ in block $j$, let $r_i={\sum }_j{n}_{ij}$, let $k_j={\sum }_i{n}_{ij}$, and let $n={\sum }_i{r}_i$. The inner product of the centered indicators for treatment $i$ and block $j$ is $n_{ij}-r_i{k}_j/n$. ConsequentlyIn particular, equal-sized blocks must contain each treatment in the same proportion. Under an additive block-and-treatment model, adjustment for blocks then does not change the fitted treatment contrasts.

Use a randomized complete block design, with day as block and each biological cell as an experimental unit. Each day should contain two biological cells at each of the five dose levels. Each level then has ten replicates overall and occurs equally often in every day: the resulting block design is an orthogonal block design.

This spreads any day-to-day changes in preparation, temperature or measurement across all levels instead of confounding dose with day. Treat the zero level as a control with otherwise comparable handling. Keep the treatment-to-measurement delay standardized because the response variable is a diffusion rate measured immediately after preparation.

If the biological cells are initially interchangeable, randomly allocate them to five groups of ten for the days. Within each day, independently choose a uniform distribution on a finite set over assignments having two occurrences of each dose level to the ten experimental units. One implementation is a random permutation of a list containing two labels of each level; the duplicate labels give every admissible assignment the same number of underlying permutations.

Randomize the processing order within each day as well, while pairing each preparation with its immediate measurement. Randomize dose within day, not merely the names of the days. This restricted randomization preserves the planned balance while protecting treatment contrasts against systematic order effects. Conceal the dose labels from the assessor where practical.

The constant subspace has one statistical degree of freedom. Day contrasts have $5-1=4$, and the within-block ANOVA stratum has $50-5=45$. Because the orthogonal block design puts all four independent dose contrasts in that last ANOVA stratum, the residual has $45-4=41$ statistical degrees of freedom.

The corrected total has 49 statistical degrees of freedom; dose is tested against the within-day residual. The quantitative dose scale also permits the dose component to be split into linear, quadratic, cubic and quartic orthogonal polynomial contrasts, each with one statistical degree of freedom. This is optional and does not assume the response is linear in dose.

The experimental unit is a volunteer on a particular afternoon, since that volunteer-session receives a program assignment. There are 36 such experimental units; a volunteer is a repeated block, rather than a unit that receives only one program throughout the experiment.

The observational unit is the individual completed sketch, equivalently the session's single recorded count of correctly represented features. The separate map features contribute to that response variable; they are not independently randomized replicates. Nor are repeated sessions on one volunteer independent subjects.

Use two crossed sets of blocks in experimental design: volunteers as rows and afternoons as columns. Volunteer blocks control persistent ability, drawing style and prior experience; afternoon blocks control conditions shared that day, including common task difficulty and general practice over time. Neither partition is nested in the other.

Give every volunteer each program twice, and use each program twice each afternoon. The row-column design is then balanced for both block systems. In the additive modelthe program contrasts are orthogonal to both centered block spaces. This controls additive volunteer and afternoon effects; it does not automatically eliminate individual learning differences or carryover effects.

Start with six program sequences: $ABCABC$, $ACBACB$, $BACBAC$, $BCABCA$, $CABCAB$ and $CBACBA$. This gives two appearances of each program per row and per column. It also balances transitions: each ordered pair of distinct programs occurs five times across all adjacent sessions.

Apply restricted randomization by randomly assigning the six sequences to the six volunteers and independently permuting the three program labels. Using the supplied numbers, rank the first six from smallest to largest: the sequence indices are $(4,1,5,2,3,6)$. Assign these, in order, to volunteers 1 through 6. Rank the next three numbers attached to symbols $(A,B,C)$: their order is $(B,C,A)$. Assign actual program labels $(A,B,C)$ to these ordered symbols, so base $A\mapsto C$, base $B\mapsto A$, base $C\mapsto B$. The final ready-to-use randomized row-column design is:

Programs retain their real identities after this label permutation. The researcher should follow the table across chronological afternoons; arbitrary column permutations are deliberately excluded so that transition balance survives. Each program receives twelve sessions and occurs twice in every block. Under the additive block model, the analysis of variance has row, column, program and residual statistical degrees of freedom $5,5,2,23$, respectively, besides the grand mean. Transition balance is useful against differential carryover effects, but is not a proof that they are absent.

Consider learning and memory of the maps. Repeating an identical map can improve later scores through recall rather than the assigned program, and a skill learned using one program can transfer to another. Provide comparable familiarization before recording responses and use new, difficulty-matched maps on later afternoons. If all volunteers face the same map on a given afternoon, common map difficulty is absorbed by the afternoon block.

The balanced transitions in the proposed row-column design help with first-order carryover effects, but general practice, higher-order memory and program-dependent learning may still require an explicit interaction term or carryover effect in the analysis. Merely applying randomization to treatment labels cannot make these effects disappear.

A completely randomized design uses $2m$ eligible animals, randomly selecting $m$ to receive $P$ and assigning the remainder to $Q$. Use comparable follow-up and assess the same response variable in both groups. Its advantage is simplicity and freedom from previous-treatment carryover effects; its disadvantage is that between-animal variation enters the residual and can make a treatment contrast imprecise.

A randomized complete block design with matched pairs first forms $m$ pairs using pre-treatment characteristics such as initial disease severity, age or breed. Independently choose which animal in each pair receives $P$, with its partner receiving $Q$. The experimental units are animals; pairs are blocks. The average within-pair difference estimates the treatment contrast, and positive within-pair similarity can reduce its variance. Its advantage is control of known heterogeneity; its disadvantage is the need for useful matching, with fewer residual statistical degrees of freedom and little gain if the matching variables are uninformative. Do not construct pairs using outcomes observed after assignment.

A two-period crossover design randomly assigns half the animals to sequence $PQ$ and half to $QP$. Each animal receives both treatments in separate periods, with a scientifically justified interval between them and the same outcome assessment after each period. Animal blocks remove persistent between-animal differences, while the two sequences balance treatment against period. Its advantage is potentially high precision from within-animal comparisons; its disadvantage is vulnerability to carryover effects, changing disease state and irreversible effects. It is suitable only when comparing the treatments in both periods remains meaningful and residual effects of the first treatment are adequately controlled. A two-period crossover design does not by itself disentangle arbitrary treatment-specific carryover effects.

First agree the scientific question and primary response variable. Ask the vet about the disease's course, the proposed mechanism and duration of each treatment, the eligible population, baseline severity, and what outcome and follow-up time would represent worthwhile improvement. Is the disease transmissible, is recovery reversible, and can treating one cow affect another's outcome? These answers determine whether a crossover design is credible, whether the experimental unit should be a cow or a whole herd, and whether individual randomization would leave interference between groups. Agree welfare and rescue arrangements with the vet when deciding which comparisons are feasible; the statistical plan cannot determine these from an unfamiliar disease name.

Second agree feasible allocation and adequate independent replication. Discuss numbers of available cows and herds, variation in the chosen outcome, a scientifically meaningful treatment difference, and the desired statistical power. Use these to plan sample size, rather than choosing a number solely from convenience. Discuss herd, lactation stage and initial severity as potential blocks in experimental design, then specify randomization, comparable management, concealed allocation and blinded outcome assessment where feasible. Repeated milk or health records from the same cow are observational units, not extra independent experimental units; pseudoreplication would give misleading standard errors. Availability of enough independent cows or herds, together with expected variation, governs the precision actually achievable.

Both factors are assigned at orchard level. Therefore the experimental units are the twelve orchards; the trees are observational units within them. The six combinations form a balanced factorial design, replicated twice. The orchard ANOVA stratum has $12-1=11$ statistical degrees of freedom. Spray uses $2-1=1$, pruning uses $3-1=2$, and their interaction term uses $(2-1)(3-1)=2$, leaving six for error.

Dividing each treatment sum of squares in ANOVA by its statistical degrees of freedom and using $1440/6=240$ as the denominator gives all missing entries:

The unrounded F-test statistics are $998/240=4.15833\dots$, $560/240=2.33333\dots$ and $202/240=0.841667\dots$. The within-orchard tree mean square in ANOVA, 180, is not the treatment error denominator: using it would confuse subsampling with independent replication. The tree ANOVA stratum has $12(30-1)=348$ statistical degrees of freedom; $1+11+348=360$ is the uncorrected total, and the corrected total is 359.

Under the usual normal linear model for independent orchard means with common error variance, the treatment ratios have null F-distributions with denominator six statistical degrees of freedom. Their upper-tail P-values are approximatelyUse the unrounded ratios when evaluating these P-values. Thus none of spray, pruning or their interaction term is significant at a 5% significance level. Spray gives modest evidence if a 10% significance level was chosen in advance, but this is not strong evidence.

Failure to reject does not establish absence of treatment effects. Only two orchards per combination and six residual statistical degrees of freedom leave considerable uncertainty and potentially low statistical power. The table alone cannot give the direction or magnitude of individual effects: that requires treatment means. These model-based F-tests also rely on appropriate orchard allocation and comparable residual variation; they should not be interpreted as unconditional conclusions from the table alone.

The orchard residual mean square in ANOVA is on the original tree-response scale: it equals 30 times the corresponding residual mean square in ANOVA for orchard means. Thus the estimated variance of one orchard's sample mean is $240/30=8$.

Each pruning marginal sample mean averages four independent orchard means, giving variance $8/4=2$. Two different pruning marginals use disjoint orchards, so the variance of their estimated treatment contrast isEach spray marginal sample mean uses six orchards. Similarly,The corresponding standard errors are $2$ and $\sqrt{8/3}$ in the units of weight per tree. These compare per-tree marginal sample means, averaging equally over the other factor, even when an interaction term is fitted. Comparing orchard totals instead would multiply these variances by $30^2$.

Report the six treatment-combination means and their uncertainty, together with useful marginal treatment contrasts, standard errors and confidence intervals. Means are needed to interpret direction and practical importance, while the fitted interaction term determines whether one factor's effects should be reported separately at levels of the other. For the pairwise marginal comparisons in part (c), ordinary model-based 95% Student t confidence intervals use $t_{6,0.975}$ times the corresponding standard error; a simultaneous set of comparisons needs an appropriate adjustment.

Also describe orchard selection, actual randomization, treatment delivery, numbers of trees observed, missing data and response units. Check orchard-level residuals for unequal variance, outliers or systematic patterns using a residual-versus-fitted plot and an appropriate distributional diagnostic. Explain that twelve orchards provide independent treatment replication; 360 tree measurements provide subsampling precision. No numerical treatment means or numerical confidence intervals can be recovered from the supplied sums of squares in ANOVA alone.

Put $a={\sigma }^2(1-\rho )$ and $c={\sigma }^2\rho$. The tree and orchard residual mean squares in ANOVA have expectations $a$ and $a+30c$. Equating these to the observed values gives the method-of-moments variance component estimatesIn particular ${\hat{\sigma }}^2=\hat{a}+\hat{c}=182$ and the estimated intraclass correlation coefficient is $\hat{\rho }=2/182=1/91$. These are point estimates from the current experiment, rather than guaranteed variance values for the next season.

Under the fitted compound-symmetry covariance model, an orchard mean based on $k$ trees has varianceWith the current estimates this falls from $v_{30}=2+180/30=8$ to $v_{45}=2+180/45=6$. The numbers of orchards contributing to each marginal remain unchanged, so both marginal treatment-contrast variances fall by a factor $6/8=3/4$: pruning differences have estimated variance $3$ and the spray difference has estimated variance $2$.

Adding trees gives a predicted 25% reduction in these variances, but no extra independent orchard replication. It requires 50% more tree measurements and leaves six orchard residual statistical degrees of freedom. Increasing $k$ reduces the $a/k$ term but cannot remove the shared orchard component $c$, so gains eventually diminish.

Allocate the extra orchards evenly, giving three independent orchards to each of the six combinations. Each orchard still has mean variance $8$ under the fitted model. Each pruning marginal now uses six orchards and each spray marginal nine, givingBoth are two-thirds of their original values. The orchard residual statistical degrees of freedom increase from $12-6=6$ to $18-6=12$.

Extra orchards improve independent replication, give a predicted one-third reduction in contrast variances, and improve error estimation. Both this option and using 45 trees require 540 tree measurements, but extra orchards offer the greater predicted statistical gain under the fitted model. They may cost more to recruit and administer; their suitability and comparability also matter.

This produces a split-plot design: assign spray to whole orchards, with six sprayed and six unsprayed, then independently randomize ten trees to each pruning method inside every orchard. Orchards remain experimental units for spray; individual trees become experimental units for pruning. Pruning contrasts and the spray-by-pruning interaction term now lie in the within-block ANOVA stratum, while spray is tested between orchards.

The between-orchard ANOVA stratum has eleven statistical degrees of freedom, split into one for spray and ten for error. The within-orchard ANOVA stratum has 348, split into two for pruning, two for the interaction term and 344 for error. This pooling of within-orchard error is appropriate under the stated compound-symmetry covariance model; additional orchard-specific pruning variation would need its own variance component rather than this simplified error model.

The shared orchard effect cancels in a pruning difference within an orchard. Its variance is $2a/10$, so averaging across twelve orchards givesThe spray contrast still compares means of six orchards per group, each based on 30 trees, so its estimated variance remains $8/3$. For a difference of pruning differences between the two spray groups, each group's pruning difference has estimated variance $2\cdot 180/(10\cdot 6)=6$, and the resulting interaction contrast has estimated variance $12$, compared with $16$ in the original allocation.

Splitting pruning within orchards improves pruning and interaction precision without extra trees, and gives spray a less sparse error estimate; it does not reduce the spray contrast's variance. This option requires tree-level pruning to be practical without interference between neighboring trees. The numerical gains, like those in the other options, assume the current variance components remain applicable next year.