Agricultural Statistics & Data Science · Design and analysis of experiments · also Advanced Design of Experiments, Recent Advances in Design of Experiments
Research-level design theory as practised at IASRI and Rothamsted: optimality of block and row-column designs, designs for correlated errors and neighbour effects, designs for bioassays and diallel crosses, supersaturated and computer-search designs, and designs for computer experiments.
In the exams: AICE-JRF Ag Stat Unit 4 (present at depth); ASRB ARS Ag Stat interview (reported); the research frontier for PhD scholars
This subject takes the design of experiments to research level. It asks which designs are best in a precise sense and how to construct designs for problems that standard layouts do not fit. It covers the optimality theory of block designs and Kiefer's universal optimality; row-column designs and their analysis; designs with neighbour effects and correlated errors; designs for diallel crosses and for factorial treatments in blocks; designs for biological assays, especially parallel-line assays; screening and supersaturated designs; orthogonal arrays and their construction; computer-aided search for efficient designs; space-filling designs such as Latin hypercube sampling for computer experiments; and the robustness of designs to missing observations.
It builds directly on the earlier design subjects of this track: the C-matrix, connectedness, BIBDs, lattices and efficiency factors from the incomplete block designs subject; confounding and fractional factorials from the factorial subject; the alphabetic optimality criteria from the response surface subject; and spatial models from the mixed-models subject. Those topics are referred to, not repeated.
In examinations, ICAR AICE-JRF/SRF Agricultural Statistics Unit 4 covers the analysis of general block designs and construction of designs at a level that leads into this material, and PhD course work and ASRB scientist interviews in agricultural statistics draw on it (as reported). Typical questions test universal optimality, the trace of the C-matrix, row-column error degrees of freedom, the definition and construction of orthogonal arrays, the numbers of runs in screening designs, parallel-line assay calculations and the properties of Latin hypercube samples.
The incomplete block designs subject measured the quality of a block design by its efficiency factor and noted that a balanced incomplete block design (BIBD) attains the upper bound v(k - 1)/[k(v - 1)]. Optimality theory, developed by Kiefer from the late 1950s, generalises this: among all designs with v treatments in b blocks of size k, which design is best, and in what sense? The answer is framed through the information matrix C = R - N K^(-1) N' and criteria that are functions of its non-zero eigenvalues: A-optimality minimises the average variance of elementary treatment contrasts (the sum of reciprocals of the eigenvalues), D-optimality maximises their product, and E-optimality maximises the smallest eigenvalue, minimising the variance of the worst-estimated normalised contrast. These are the same alphabetic criteria met in the response surface subject, now applied to treatment comparisons in blocks.
Kiefer (1975) showed that a design whose C-matrix is completely symmetric (all diagonal elements equal and all off-diagonal elements equal) and has the maximum trace among all competing designs is universally optimal: it is optimal for every criterion in a broad class that includes A, D and E. For binary designs with b blocks of size k, the trace of C is b(k - 1), which is the maximum possible; a BIBD has a completely symmetric C equal to (lambda v / k)(I - J/v), so whenever a BIBD exists it is universally optimal among all designs with the same v, b and k. For example, in the BIBD with v = b = 7 and k = 3, the trace of C is 7 x 2 = 14, equal to (7/3) x 6. When block size exceeds the number of treatments, Kiefer's balanced block designs (in which each treatment appears either floor(k/v) or floor(k/v) + 1 times in each block, with balance) play the same role. When no BIBD exists, optimal designs are sought among near-balanced designs, regular graph designs (whose concurrences differ by at most one) and computer-generated designs; for small cases optimal designs are tabulated, and for practical sizes efficient designs close to the bound are found by search (chapter 8).
Many experiments compare several test treatments with a control rather than all pairs. Designs that are optimal for all pairwise comparisons are not optimal for this purpose; balanced treatment incomplete block designs (BTIBDs), introduced by Bechhofer and Tamhane, give every test treatment the same variance of comparison with the control and are A-optimal for these contrasts in many cases. They typically include the control more often than the test treatments, sometimes several times per block, which reflects the general principle that the optimal design depends on the contrasts of interest.
Consider v = 4 treatments in b = 6 blocks of size 2. The unreduced BIBD (all six pairs, lambda = 1) has C = (lambda v / k)(I - J/4) = 2(I - J/4), with non-zero eigenvalues 2, 2 and 2, so every elementary contrast has variance 2 sigma squared / 2 = sigma squared. An alternative design that repeats the pairs {1, 2} and {3, 4} three times each is disconnected: its C-matrix has a zero eigenvalue for the contrast between the two groups, and the A-, D- and E-criteria all register it as infinitely bad. A third design with pairs {1, 2}, {1, 2}, {2, 3}, {3, 4}, {3, 4}, {4, 1} is connected but unbalanced, and its eigenvalues are unequal, so its average variance is larger than the BIBD's. The example shows why complete symmetry with maximal trace wins under every criterion.
Exact optimality results apply to idealised models (fixed blocks, independent errors with constant variance). Real trials analysed with random blocks, spatial correlation or unequal variances may favour slightly different designs. Optimality theory therefore guides design choice by identifying excellent designs and upper bounds, while practical design generation also considers resolvability, field shape, robustness and the expected size of block and spatial effects.
Because the A-criterion of any design with v treatments in blocks of size k cannot beat that of a BIBD with the same parameters, the BIBD bound v(k - 1)/[k(v - 1)] serves as a benchmark for every candidate design, whether or not a BIBD exists. Tighter bounds that account for the impossibility of a BIBD for given parameters have been derived, and design software reports efficiency relative to such bounds. A design within one or two per cent of the bound is, for practical purposes, optimal.
A row-column design arranges v treatments in a p x q array of experimental units, with rows and columns as two crossed blocking factors, generalising the Latin square and the Youden square of the earlier design subjects. Rows and columns may each be incomplete with respect to treatments. Writing N_r and N_c for the treatment-by-row and treatment-by-column incidence matrices, the information matrix for treatments adjusted for rows and columns is C = R - (1/q) N_r N_r' - (1/p) N_c N_c' + (1/pq) r r', where r is the vector of replications; this form holds for designs in which rows and columns are orthogonal to each other, as in a complete array. The error degrees of freedom of a connected row-column design are pq - p - q - v + 2; for 24 plots in 4 rows and 6 columns with 12 treatments, they are 24 - 4 - 6 - 12 + 2 = 4.
Generalised Youden designs, in which every treatment occurs equally often in every row (or as nearly so as possible) and the column component is balanced, are universally optimal row-column designs in Kiefer's sense when they exist. For field trials with many entries, resolvable row-column designs (replicates divided into rows and columns of plots) and latinized designs, in which each treatment occurs once in each long column of the field across replicates, are produced by search algorithms. Their analysis is a mixed-model analysis with random row and column effects within replicates, often combined with spatial correlation as in the mixed-models subject. Row-column designs also suit glasshouse benches (bench rows and positions), laboratory runs (days and positions) and animal experiments (animals and periods).
In the intra-block analysis of a row-column design, rows and columns are eliminated and treatments adjusted for both; the reduced normal equations C tau-hat = Q use adjusted totals Q = T - (1/q) N_r R_tot - (1/p) N_c C_tot + (G/pq) r, where R_tot and C_tot are the row and column totals and G the grand total. When rows are complete (each treatment once per row), as in a Youden square, row adjustments vanish from treatment comparisons and only the column adjustment remains, as noted in the incomplete block designs subject. Modern practice fits rows and columns as random effects by REML, recovering information from both directions.
A breeding trial of 120 entries in two replicates is laid out as a grid of 12 rows by 20 columns. A resolvable row-column design makes each replicate a block of 12 rows by 10 columns, with entries arranged so that pairs of entries rarely share both a row and a column. Analysis includes replicates, rows within replicates and columns within replicates as random effects and a spatial residual if the variogram suggests it. Compared with an RCBD analysis with replicates only, the row-column analysis often reduces the average standard error of entry differences substantially in variable fields.
In a latinized design, the replicates are laid side by side as long columns of the field, and the design ensures that each treatment appears once in each long column across the trial, or in each row across replicates, in addition to the blocking within replicates. This protects against trends running the full length of the field, which within-replicate blocks cannot capture. Latinization costs little efficiency and is now standard in many variety-testing programmes.
In field trials the response of a plot can be affected by its neighbours: a tall variety shades a short one, an aggressive variety competes for water and nutrients, a fungicide drifts, or a disease spreads from a susceptible neighbour. Such neighbour (interference) effects bias treatment comparisons unless controlled. Guard rows and wider plots reduce them. When they cannot be avoided, neighbour-balanced designs arrange treatments so that each treatment has every other treatment as a left and right neighbour equally often (or as nearly so as possible), allowing direct and neighbour effects to be estimated separately by least squares. Circular neighbour-balanced designs, with border plots at the ends of each block repeating the treatments at the opposite end, were developed by Azais, Bailey and Monod (1993) among others. Grouping varieties of similar height or maturity in the same trial is a practical complement.
When plot errors are spatially correlated, as discussed for spatial analysis in the mixed-models subject, the efficiency of a design depends on the correlation structure as well as on blocking. Designs efficient under first-order autoregressive or nearest-neighbour correlation tend to place each treatment next to as many different treatments as possible and to avoid placing the same treatment in adjacent plots. Work by Martin, Kiefer and Wynn and others shows that some systematic-looking arrangements are highly efficient under specific correlation models. In practice, randomisation is retained to protect validity, and the design is chosen from among randomised layouts with good neighbour properties; the analysis then uses an appropriate spatial model. Nearest-neighbour balance and spatial efficiency are therefore design criteria that complement, not replace, randomisation.
With four treatments in a single line of plots, a neighbour-balanced sequence (with border plots at each end) is arranged so that each treatment has each of the others as its left neighbour, and as its right neighbour, equally often; such sequences are found from tables or by search, and simply writing the treatments in a few different orders rarely achieves balance. In such a design, the response of each plot can be modelled as direct effect of its treatment plus left and right neighbour effects; least squares then estimates direct effects free of neighbour bias. Without neighbour balance, a treatment that happened to sit beside a strong competitor more often would be unfairly penalised.
Neighbour effects matter most in single-row or narrow-plot trials, between genotypes differing in height, earliness or vigour, in trials of herbicides and fungicides where drift or spread occurs, and in disease trials with inoculum moving between plots. Where guard rows are cheap, they remain the simplest remedy; where plots must be small, as in early-generation breeding, neighbour-balanced or neighbour-aware designs and analyses are valuable.
Neighbour-balanced arrangements constrain randomisation, since only a subset of all possible layouts has the balance property. Randomisation within that subset (for example by randomly relabelling treatments and reversing or rotating sequences) preserves validity for the analysis that takes neighbour effects into account. The same idea, restricted randomisation, appears in Latin squares and other constrained designs.
A complete diallel cross of p parents involves p(p - 1)/2 crosses (Griffing's method 4), 28 for 8 parents and 45 for 10, as discussed in the biometrical techniques subject. Laying all crosses out in complete blocks gives large, heterogeneous blocks, and early work treated the crosses as treatments in an RCBD regardless. Optimal block designs for diallel crosses, studied by Gupta, Das and Kageyama, Dey and Midha and others, treat the crosses as treatments whose responses depend on the general combining abilities (GCA) of the two parents, and choose incomplete blocks so that GCA comparisons are estimated as precisely as possible. Partial diallel crosses (Kempthorne and Curnow, 1961), in which each parent is crossed with only s others, reduce the number of crosses when p is large, at the cost of less information on specific combining ability.
The factorial subject showed how confounding sacrifices chosen interactions to keep blocks small. A more general theory considers block designs whose treatments have factorial structure and asks which effects are estimated with what efficiency. A design has orthogonal factorial structure (OFS) when the adjusted treatment sums of squares split orthogonally into main effects and interactions; with balance, each effect has its own efficiency factor, and partial confounding appears as efficiency factors below one. Kronecker product designs, built from block designs for each factor separately, give OFS with known efficiency factors. Choosing a design then means choosing which effects to estimate precisely, as in confounding, but with a wider menu of block sizes and replication patterns.
For p = 8 parents, a complete diallel without parents or reciprocals has 28 crosses and estimates 7 GCA contrasts and 20 SCA effects (28 - 7 - 1). If blocks can hold only 7 plots, a design that places crosses so that each pair of parents' GCA comparison is equally precise is needed; such designs come from BIBDs or PBIBDs whose treatments are the crosses, chosen so that parent concurrences are balanced. A partial diallel with s = 3 crosses per parent needs only 8 x 3 / 2 = 12 crosses, sacrificing most SCA information but keeping GCA estimates.
In a 3 x 4 factorial laid out in blocks of 6 plots, a Kronecker product design can give main effects of the first factor full efficiency and spread the loss over the interaction and the second factor's main effect in known proportions. The experimenter chooses which effects matter most, just as in confounding, but with exact efficiency factors to compare alternative designs.
In breeding programmes, diallel crosses among 6 to 12 parents are common, and the crosses are often evaluated at several sites. The design question then has two parts: the block design within each site, chosen to compare GCA effects efficiently, and the allocation of crosses across sites, which in sparse testing may test each cross at only some sites. Mixed models with GCA and SCA as random effects and site interactions analyse the combined data.
A biological assay estimates the potency of a test preparation (a vitamin, hormone, vaccine, insecticide, antibiotic) relative to a standard by comparing the responses of living material to graded doses of each. In a direct assay the dose needed to produce a specified effect is measured directly; in an indirect assay, responses to fixed doses are measured and the relative potency is estimated from the dose-response relationships. Quantal responses (death or survival) are analysed by probit or logit models, as discussed in the bioassay and survival subject; this chapter concerns the designs for quantitative-response assays.
In a parallel-line assay, the response is linear in log dose for both preparations, and if the test preparation behaves like a dilution of the standard the two lines are parallel; the horizontal distance between them is the log relative potency M. If the lines have common slope b, M = (y-bar_T - y-bar_S)/b + (x-bar_S - x-bar_T), where y-bar and x-bar are the mean responses and mean log doses. If both preparations are tested at doses with the same mean log dose, y-bar_T = 52, y-bar_S = 48 and b = 20 per unit of log10 dose, then M = 0.2 and the potency ratio is 10^0.2 = 1.58. In a symmetric (k, k) assay, each preparation is given at k doses in the same ratio; the (2, 2) four-point and (3, 3) six-point assays are common. The treatment sum of squares splits into orthogonal contrasts for preparations, regression, parallelism (deviation from parallel lines) and, with three or more doses, curvature; validity requires significant regression and non-significant parallelism and curvature. Confidence limits for the potency use Fieller's theorem because M is a ratio. In a slope-ratio assay, the response is linear in dose (not log dose) with a common intercept for both preparations, and the relative potency is the ratio of slopes. When blocks (litters, plates, days) cannot hold all doses of both preparations, incomplete block designs for parallel-line assays (Das, Kulkarni and others) confound unimportant contrasts such as curvature differences with blocks while keeping the preparation, regression and parallelism contrasts clear.
In a symmetric (3, 3) parallel-line assay with r replicates per dose, the 5 degrees of freedom for treatments split into preparations (1), regression (1), parallelism (1), curvature (1) and difference of curvature (1). The assay is valid when regression is highly significant and parallelism and both curvature terms are non-significant; otherwise the log-dose transformation or the assumption that the test behaves like a dilution of the standard is questionable. Only then is the potency estimated from the preparations and regression contrasts.
When an animal litter or culture plate can receive only four of the six doses of a (3, 3) assay, incomplete block designs are chosen so that the preparation, regression and parallelism contrasts are estimated with full efficiency and the curvature contrasts are partly confounded with blocks. This mirrors confounding in factorial experiments: the contrasts least needed for the potency estimate absorb the block effects.
For quantal responses, the proportion of insects killed or plants infected at each dose is modelled by probit or logit regression on log dose, and the LD50 or relative potency is estimated from the fitted lines; parallelism of the standard and test lines is again required. Designs place doses so that expected responses span roughly 20% to 80%, where the information about the LD50 is greatest, a principle also used in sequential up-and-down designs.
Screening experiments identify the few important factors among many candidates. Two-level fractional factorials of resolution III and Plackett-Burman designs (1946), built from Hadamard matrices, estimate N - 1 main effects in N runs, where N is a multiple of four: a 12-run Plackett-Burman design screens up to 11 factors. They rely on effect sparsity (few factors matter) and assume interactions are small or accept that they are partially aliased with main effects. Definitive screening designs (Jones and Nachtsheim, 2011) use three levels and 2m + 1 runs for m factors, estimating main effects free of two-factor interactions and allowing curvature to be detected.
A supersaturated design has fewer runs than the number of effects to be estimated (k factors with N - 1 < k), so not all main effects can be estimated simultaneously. Introduced by Satterthwaite (1959) as random balance and given a systematic basis by Booth and Cox (1962), supersaturated designs are chosen to make the columns as nearly orthogonal as possible, commonly by minimising E(s squared), the average squared inner product between pairs of columns. Lin (1993) constructed them from half-fractions of Hadamard matrices. Analysis uses methods that exploit sparsity, such as stepwise selection, penalised regression or Bayesian variable selection, and results must be confirmed by follow-up experiments. In agriculture, they suit preliminary screening of many medium components, cultivation factors or management practices where runs are expensive.
A tissue-culture laboratory wants to know which of 11 medium components affect regeneration. A 12-run Plackett-Burman design tests all 11 main effects, assuming interactions are small; significant components are then studied in a follow-up factorial or response surface design. If 20 components were candidates and only 12 runs were affordable, a supersaturated design would be needed, accepting that some main effects are correlated and that conclusions must be confirmed.
Because the model matrix has more columns than rows, ordinary least squares cannot fit all main effects. Forward selection, the lasso and Bayesian variable-selection methods identify a small set of active factors, and simulation studies show they work reasonably when only a few factors are active and their effects are large. With many active factors, supersaturated designs are unreliable, which is why they are used only for early screening.
For six three-level factors, a definitive screening design has 13 runs: pairs of fold-over runs and one centre run. Main effects are orthogonal to each other and to all two-factor interactions and quadratic terms, and if only a few factors are active the design can estimate a full quadratic model in them. These properties make definitive screening designs attractive for process and formulation work where curvature is expected.
Screening is the first stage of a sequence: once a few active factors are identified, a full or fractional factorial in those factors estimates interactions, and a response surface design locates the optimum, as in the response surface subject. Planning the sequence from the start helps choose screening designs whose runs can be reused in later stages.
An orthogonal array OA(N, k, s, t) is an N x k array with entries from s symbols such that, in every N x t sub-array, each of the s^t possible t-tuples occurs equally often, lambda = N / s^t times; N is the number of runs, k the number of factors, s the number of levels and t the strength. Rao (1947) introduced orthogonal arrays and showed their role in fractional factorials: an array of strength 2 gives orthogonal estimates of main effects when interactions are negligible, and strength 3 protects main effects from two-factor interactions. Taguchi's L8, L9, L16 and L18 arrays, used in the response surface subject, are orthogonal arrays. For example, OA(9, 4, 3, 2), the L9, accommodates four three-level factors in nine runs with index lambda = 9/3^2 = 1.
Several classical constructions exist. From a Hadamard matrix of order 4 lambda (an orthogonal matrix of plus and minus ones), deleting the first column after normalisation gives OA(4 lambda, 4 lambda - 1, 2, 2), the Plackett-Burman designs. From a Galois field GF(s) with s a prime power, the Rao-Hamming construction gives OA(s^n, (s^n - 1)/(s - 1), s, 2): for s = 3 and n = 2, OA(9, 4, 3, 2). From a complete set of s - 1 mutually orthogonal Latin squares of order s, OA(s squared, s + 1, s, 2) is obtained by taking row, column and the letters of each square as columns, which links orthogonal arrays to the lattice designs of the incomplete block designs subject. Bush's construction uses polynomials over GF(s) for higher strength. Rao's bound gives a lower limit on N for given k, s and t; arrays attaining it are called tight. Mixed-level arrays (such as L18 with one two-level and seven three-level columns) are built by combining these methods.
To check that an array has strength 2, look at every pair of columns and count each of the s squared level combinations; they must all occur lambda = N/s squared times. For OA(8, 7, 2, 2), each pair of columns contains (0, 0), (0, 1), (1, 0) and (1, 1) exactly twice. A strength-3 array OA(16, 8, 2, 3) has each triple of columns containing all eight combinations twice, so it supports a resolution IV fraction for 8 factors in 16 runs.
Orthogonal arrays unify several earlier topics: two-level fractional factorials are orthogonal arrays; complete sets of mutually orthogonal Latin squares are equivalent to orthogonal arrays of strength 2 with s + 1 columns; and resolvable BIBDs such as balanced lattices can be read from them. Their use in computer experiments, as orthogonal-array-based Latin hypercubes, gives designs with good low-dimensional projections.
Real experiments often combine factors with different numbers of levels, such as two varieties, three nitrogen rates and four sowing dates. Mixed-level orthogonal arrays accommodate these, for example arrays in 16 runs with one four-level and several two-level columns obtained by replacing three two-level columns (two columns and their interaction) by one four-level column. Tables of such arrays are available, and computer search finds nearly orthogonal arrays when exact ones do not exist.
BIBDs and other balanced designs exist only for limited parameter sets, while practical experiments have fixed numbers of treatments, replicates, block sizes and field shapes. Computer search finds designs whose efficiency factors (or A- or D-criteria) are close to the theoretical upper bounds of chapter 1. Search methods include exchange and interchange algorithms (swapping treatments between plots or blocks while the criterion improves), simulated annealing (accepting occasional worse moves to escape local optima) and tabu search. Algebraic starting points such as cyclic or alpha designs are often improved by search.
For block designs the usual criterion is the A-efficiency of elementary contrasts, sometimes with constraints such as resolvability, a minimum or maximum concurrence, or spatial properties such as avoiding adjacent repeats of a treatment. For row-column and resolvable designs, efficiency is computed for both the row and the column components or for a mixed model with assumed variance ratios, since the best design depends on how large block or spatial effects are expected to be. Design-generation software for agricultural trials implements these ideas, and its output should be checked: the efficiency factor relative to the upper bound, the range of pairwise variances, the randomisation of the final layout, and whether the design meets practical constraints such as machinery and seed lots. Reporting the design's efficiency and the software used makes the trial reproducible.
Suppose 30 entries must be tested in three replicates of six blocks of five plots. No BIBD exists, but an alpha design gives an efficiency factor of perhaps 0.79 against an upper bound of 0.83 (as noted in the incomplete block designs subject). A simulated-annealing search that swaps entries between blocks within replicates may raise this slightly and can simultaneously ensure that no two entries share a block more than once. The gain may be small, but the search also checks constraints that algebraic constructions ignore.
When the analysis will be a mixed model with assumed variance ratios for blocks, rows, columns and spatial correlation, the design can be chosen to minimise the expected average variance of entry differences under that model. Such model-based designs are particularly useful for large breeding trials, partially replicated designs and designs that combine several sites, and the assumed variance ratios can be taken from previous trials on the same station.
A design generated by search depends on the algorithm, its settings and the random seed. Recording these, with the final layout and its efficiency, lets others reproduce or audit the design and is part of good reporting, alongside the randomisation plan required for any experiment.
Computer experiments run a deterministic simulator, such as a crop growth model, hydrological model or epidemiological model, at chosen input settings. They differ from physical experiments: there is no random error (repeating a run gives the same output), so replication, randomisation and blocking are irrelevant, and the aim is to explore the input space efficiently and to build a cheap statistical approximation (an emulator) of the expensive simulator. Designs are therefore space-filling, spreading points throughout the input region rather than placing them at the edges as optimal designs for polynomial models do.
Latin hypercube sampling (McKay, Beckman and Conover, 1979) divides the range of each of d inputs into n equal intervals and chooses n runs so that each interval of each input is used exactly once: the design is n points such that their projections onto every single input are evenly spread. A random Latin hypercube pairs the intervals of different inputs at random; for n = 10 runs and 3 inputs, each input takes one value in each tenth of its range. Random Latin hypercubes can still cluster in two or more dimensions, so improved versions are used: maximin Latin hypercubes maximise the minimum distance between points, orthogonal or nearly orthogonal Latin hypercubes minimise correlations between inputs, and sliced and nested designs serve multi-fidelity and sequential use. The output is typically modelled with a Gaussian process (kriging) emulator, whose correlation function interpolates the runs exactly and provides uncertainty for predictions elsewhere; global sensitivity analysis (for example Sobol indices) then identifies which inputs drive the output. In agriculture, these methods are used to calibrate crop models, to explore climate-change scenarios and to quantify uncertainty in model-based yield forecasts.
For 5 runs and 2 inputs on [0, 1], divide each input into five intervals of width 0.2. A Latin hypercube takes one value in each interval for each input, for example interval midpoints 0.1, 0.3, 0.5, 0.7 and 0.9, and pairs them by a random permutation, such as (0.1, 0.7), (0.3, 0.1), (0.5, 0.9), (0.7, 0.3) and (0.9, 0.5). Every input's one-dimensional projection is perfectly spread, whereas a simple random sample of five points might leave large gaps. A maximin version would choose, among many permutations, the one maximising the smallest distance between any two points.
Calibrating a crop model with ten uncertain parameters by running every combination of three levels would need 3^10 = 59,049 runs; a Latin hypercube of a few hundred runs, an emulator fitted to them and Bayesian calibration against field data make the task feasible. The same approach quantifies how uncertainty in soil and weather inputs propagates to yield forecasts, supporting the model-based forecasting described in the crop forecasting subject.
Running a deterministic simulator twice at the same inputs gives the same output, so replication wastes runs and blocking is meaningless. Uncertainty in computer experiments comes from not knowing the output between design points and from uncertainty about the simulator's inputs and its agreement with reality, which emulators and calibration address. If the simulator is stochastic, replication again becomes relevant.
Rather than choosing all runs at once, sequential designs add runs where the emulator is most uncertain or where the output is most interesting (for example near an optimum or a threshold). Such adaptive strategies make efficient use of expensive simulators and are widely used in engineering and increasingly in agricultural modelling.
Plots are lost to floods, pests, animal damage and errors; in animal experiments, animals die or are removed. The basic designs subject treated missing plots by estimation formulas and the mixed-models subject by likelihood analysis of the remaining data; both assume the remaining design is still adequate. A design is robust if it remains connected, and loses little efficiency, when some observations are lost. Some designs are fragile: in a design where two treatments occur together in only one block, losing that block may disconnect them or sharply reduce the precision of their comparison.
Robustness is studied by examining the efficiency of the residual design after deleting any single observation, any t observations, or any whole block, and reporting the minimum or average efficiency. Ghosh and others showed that BIBDs are robust in the sense that the loss of any one block (or any one observation) leaves a connected design with high efficiency, and characterised how many observations can be lost before connectedness may fail. Designs with higher replication and more evenly spread concurrences are generally more robust. In practice, robustness is one reason to prefer designs with some spare replication, to avoid designs that rely on a single concurrence for critical comparisons, and, in variety trials, to use resolvable designs, which remain analysable as complete replicates even when one replicate is lost. Computer search can include a robustness constraint, such as requiring that the design stays connected after the loss of any one block.
In a design for 6 treatments in blocks of 3 in which treatments 1 and 6 occur together in only one block and are linked to the others mainly through that block, the loss of that block can sharply reduce the precision of comparisons involving 1 and 6. A BIBD with v = 6, k = 3, lambda = 2 (r = 5, b = 10) puts every pair together twice, so the loss of any one block leaves every pair still concurring at least once and the design connected with only a modest loss of efficiency.
Choose designs with at least moderate replication, prefer designs in which every pair of treatments concurs at least once where possible, check the efficiency of the design after deleting each block in turn (a simple computation), and in long or risky experiments add spare replication or reserve plots. Report missing data and analyse with methods valid for the remaining design, such as mixed models.
Animal experiments lose units through death or culling, and long-term or perennial experiments lose plots over years. Designs for such settings should anticipate losses by adding spare replication, by preferring designs that remain balanced in large subsets, and by planning analyses (mixed models) that use all remaining data. The ethical aim of using no more animals than necessary has to be balanced against the risk that losses leave the experiment unable to answer its question.
Every report should state how many observations were lost, where, and why, so that readers can judge whether losses were random and whether the remaining design supports the conclusions.
PhD students in agricultural statistics take this as an advanced course and often choose a thesis in it: constructing optimal or robust designs, designs for diallel crosses or bioassays, or space-filling designs for crop-model studies. They must understand the C-matrix criteria, prove simple optimality results and construct designs from finite fields and Latin squares.
A five-year design statistician generates designs for breeding networks, bioassay laboratories and simulation studies: row-column and latinized designs for large trials, neighbour-balanced layouts for trials with tall and short entries, efficient designs for diallel crosses, and Latin hypercubes for crop-model calibration, checking efficiency and robustness before release.
A senior statistician sets design policy for institutions: which design families and software are standard, minimum efficiency and robustness requirements, and how new methods (spatially efficient designs, model-based designs for genomic selection trials) are adopted.
A PhD with long experience contributes to design theory itself (new constructions, optimality results, designs for new settings) and is consulted on the hardest design problems of national and international programmes.
Proofs of universal optimality, of the row-column information matrix and of orthogonal-array bounds are outlined only. Detailed theory of neighbour-balanced designs, optimal designs for diallel crosses and robustness results are described with the main references, not derived. Software for design generation is mentioned generically. Bioassay calculations are shown for the simplest parallel-line case; Fieller intervals are not worked.
Original practice questions written to the syllabus and pattern of the exams named in each question's examTags. They are not past papers and do not reproduce any board's questions. Every numerical answer was computed with a script; the values needed are stated in the question.
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