Agricultural Statistics & Data Science · Design and analysis of experiments · also Design of Experiments I, Field Plot Technique, Experimental Designs (minor course)
Fisher's three principles and how they shape a field or animal trial: uniformity trials, plot size and shape, the CRD, RCBD and Latin square with their analysis and efficiency, missing plots, transformations, multiple comparisons and analysis of covariance.
In the exams: AICE-JRF Ag Stat Unit 4 (heavy); AIEEA-PG Group 07 (CRD, RBD named); AICE-JRF Agronomy Unit 6 (heavy); ASRB NET Ag Stat (heavy); UPSC ISS Statistics III (present)
Design of experiments is the part of statistics that decides, before any seed is sown or animal fed, how a comparison will be made so that its result is unbiased and precise enough to be useful. This manual covers the basic designs and techniques that every agricultural statistician, agronomist, breeder and animal scientist uses: Fisher's three principles of replication, randomisation and local control; soil heterogeneity, uniformity trials and the choice of plot and block size and shape, including Smith's variance law; the completely randomised, randomised complete block and Latin square designs with their analysis of variance; relative efficiency; missing plots; the assumptions of the analysis and variance-stabilising transformations; multiple comparison procedures; the analysis of covariance; and the number of replications.
The subject was born in agriculture. Fisher developed the analysis of variance and the principles of design at the Rothamsted Experimental Station in the 1920s, and Yates, Cochran, Panse and Sukhatme carried the methods into field research worldwide. Today the same ideas are used in every field, greenhouse, animal and laboratory experiment, and they are examined everywhere agricultural statistics is taught.
In examinations the subject is heavy. The completely randomised and randomised block designs are named in the statistics unit of ICAR AIEEA-PG Group 07; the whole of this manual sits inside Unit 4 Design of Experiments of the ICAR AICE-JRF/SRF Agricultural Statistics syllabus and the statistics unit of AICE-JRF Agronomy; ASRB NET and ARS papers in agricultural statistics draw on it; and design of experiments is reported in the Indian Statistical Service papers. Numerical questions typically ask for degrees of freedom, a sum of squares, F, a critical difference, a coefficient of variation, a relative efficiency or a missing-plot estimate, so each chapter gives the formula in words and the manual's question bank works these numbers.
Factorial experiments, split- and strip-plot designs, incomplete block designs, response surfaces, multi-location trials and mixed models build on this foundation and have their own manuals in this track.
A comparative experiment applies chosen treatments to experimental units and measures a response, so that differences between treatments can be estimated and tested. A treatment is whatever the experimenter controls: a variety, a fertiliser dose, an irrigation schedule, a feed ration or a spray. The experimental unit is the smallest piece of material to which one treatment is applied independently of the others: a field plot, a pot, a pen of birds, an individual cow or a Petri dish. The response is what is measured on each unit, such as grain yield, plant height, milk yield or the number of insects. Two further words prevent much confusion. A sampling unit, or observational unit, is a part of an experimental unit on which a measurement is taken: five plants inside a plot, or three leaves on a plant. Measurements on sampling units are not replications of a treatment, because they share the same application of that treatment; treating them as if they were is called pseudo-replication and makes the error look much smaller than it is. Experimental error is the variation among experimental units that receive the same treatment. It arises from soil differences, genetic differences between animals, small differences in management and measurement error, and it is the yardstick against which treatment differences are judged. A design is the plan that decides how many units there are, how they are grouped, and which treatment goes to which unit. Design is decided before the experiment. Analysis can recover a little from a poor design but cannot repair a missing comparison, a confounded effect or a biased allocation. That is why statisticians ask to be consulted at the planning stage rather than when the data arrive.
Replication means applying each treatment to more than one experimental unit. It has two jobs. First, it provides an estimate of experimental error: with only one unit per treatment there is no way to know how much two units given the same treatment would differ, so no test of significance is possible. Second, it increases precision. If the error variance per unit is sigma squared, the variance of a treatment mean based on r replications is sigma squared divided by r, so the standard error of a mean falls in proportion to one over the square root of r, and the standard error of the difference between two means is the square root of 2 sigma squared over r. Doubling replication does not halve the standard error; it divides it by about 1.41, and replication must be quadrupled to halve it. Replication also widens the range of conditions over which results apply, especially when the replications are spread over blocks that differ. In field research it is common to replicate within a site and then repeat the experiment across sites and seasons, but those repetitions answer a different question (consistency over environments) and are analysed as groups of experiments, not as extra replicates.
Randomisation means allocating treatments to experimental units by a random process, such as random numbers from a table or a computer, so that every unit has a known and equal chance of receiving each treatment within the restrictions of the design. R. A. Fisher, who built the modern theory of experimental design at the Rothamsted Experimental Station and set it out in The Design of Experiments (1935), insisted on randomisation for two reasons. It removes systematic bias: no treatment is favoured by being placed, consciously or not, on the better soil, the healthier animals or the bench nearest the window. And it makes the estimate of error valid: because each treatment is equally likely to land on any unit, the errors behave as if independent, so the F and t tests have their stated properties. A systematic arrangement such as always putting treatment A next to treatment B in the same order can be more convenient, and sometimes looks tidier, but it may coincide with a fertility trend or a drainage line and produce a biased comparison and a biased error. Randomisation does not make every single layout good; it makes the procedure fair on average and gives the statistical tests their justification.
Local control is the use of grouping, blocking or balancing to reduce experimental error. Units that are alike are put into a group (a block), each group receives every treatment, and the variation between groups is removed from the error in the analysis. In a field with a slope or a fertility gradient, blocks are laid across the gradient so that the plots within a block are similar; in an animal trial, animals of similar initial weight or the same litter form a block; in a laboratory, the batch processed on one day can form a block. Local control is the principle that separates the randomised block and Latin square designs from the completely randomised design. Its cost is a loss of error degrees of freedom, because some degrees of freedom are spent estimating block effects. It pays when blocks really differ, and the relative efficiency calculations in a later chapter measure whether it did. Fisher's three principles work together: replication supplies an error estimate, randomisation makes it valid and unbiased, and local control makes it small.
No field is uniform. Fertility differs because of past cropping, manure heaps, levelling, drainage, slope, erosion, depth of the soil and the shade or root competition of trees and bunds. Variation also comes from the experimenter: uneven sowing, irrigation that reaches one end first, or harvesting by different teams. Some of this variation is patchy and some follows a gradient, such as fertility falling steadily down a slope or away from an irrigation channel. Soil heterogeneity is the main source of experimental error in field trials. Designing a trial well means knowing roughly how large it is and in which directions it runs, so that plot size, plot shape, block shape and block orientation can be chosen to keep it out of treatment comparisons. Previous trials on the same land, visual observation of an earlier crop and, most systematically, uniformity trials provide this knowledge.
A uniformity trial, or blank trial, grows one variety over the whole experimental area with uniform management throughout, then harvests it in small basic units of equal size, for example a grid of plots of one square metre or one row length each. Because no treatments were applied, the differences between basic units measure soil heterogeneity and other uncontrolled variation. The yields of the basic units are used in several ways. Adjacent units are combined into larger plots of different sizes and shapes, and the variance and coefficient of variation of each plot size are calculated; this shows how error changes with plot size and shape and leads to the choice of an optimum plot size. Combining units in different directions shows whether long narrow plots or square plots are more uniform, and in which direction blocks should run. The correlation between yields of neighbouring units shows how strongly fertility is spatially patterned. The data also give an estimate of the number of replications needed for a stated precision. The main drawback is cost: a whole season is spent on land and labour without testing any treatment, and the pattern found in one season with one crop may not hold for another. For this reason uniformity trials are run when a new research farm is opened, or the data from the first experiments on new land are analysed for heterogeneity instead.
A fertility contour map is drawn from the yields of the basic units of a uniformity trial. Because individual basic-unit yields are noisy, they are first smoothed, typically by replacing each value with the moving average of a small block of neighbouring units. Lines are then drawn through points of equal smoothed yield, in the same way that contour lines on a topographic map join points of equal height. The map shows at a glance whether productivity rises in one direction (a gradient, seen as roughly parallel contour lines), in two directions, or in patches (closed contours). A unidirectional gradient calls for blocks laid across it; a two-directional pattern suggests a Latin square or row-and-column blocking; patchy heterogeneity suggests smaller blocks or incomplete block designs. The map is also used to keep trials off unusual patches such as old threshing floors or filled ditches.
As plots get larger they average over more soil, so the variance of yield per unit area falls and the coefficient of variation decreases. It does not fall in proportion to plot size, however, because neighbouring pieces of land are positively correlated: adding a neighbouring strip brings in soil that is similar to what is already in the plot. The decline in variance is therefore steep at first and flattens out as plots grow, and beyond some size larger plots buy little extra precision while costing more land, seed and labour and making blocks larger and less homogeneous. Practical limits also set plot size: the machinery used for sowing and harvesting, the need for border rows, the amount of seed available for new breeding lines (which forces small plots in early-generation trials), and the type of crop. Tall crops and those with wide spacing need larger plots than closely spaced short crops.
H. Fairfield Smith (1938) found that, in uniformity-trial data, the variance of yield per basic unit for plots of x basic units follows the empirical relation V(x) = V(1) / x to the power b, where V(1) is the variance among single basic units and b is the index of soil heterogeneity. Taking logarithms gives log V(x) = log V(1) - b log x, a straight line, so b is estimated as the negative of the slope of log variance against log plot size, or from two plot sizes as b = log(V(1)/V(x)) / log x. The value of b lies between 0 and 1. When b is close to 1, yields of adjacent units are nearly uncorrelated, so variance per unit falls almost in proportion to plot size and larger plots are an efficient way to reduce error. When b is close to 0, adjacent units are highly correlated and enlarging plots hardly reduces the variance; more replications of smaller plots are then better. Smith also showed how the optimum plot size depends on costs: if K1 is the part of the cost that is proportional to the number of plots and K2 is the part proportional to total area, the plot size that gives the greatest precision per unit cost is x = b K1 / ((1 - b) K2) basic units. The law is empirical. Its fit and the value of b differ between fields, crops and seasons, and b also depends on the shape in which basic units are combined, so it should be estimated from local data.
When fertility changes in one direction, long and narrow plots laid with their long side along the gradient each sample the whole range of fertility, so they differ less from one another than square plots would. Long narrow plots also suit machinery and irrigation channels. Their drawback is a larger perimeter relative to area, so border effects matter more, and border rows must be discarded at harvest. Square plots have the smallest perimeter for a given area and are preferred when the heterogeneity has no clear direction or when border effects are large. Blocks follow the opposite logic. The aim is that plots within one block are as alike as possible and that the differences go between blocks. With a unidirectional gradient, blocks are therefore laid as long strips with their long side across (perpendicular to) the gradient, and the blocks are arranged one after another along the gradient. Gomez and Gomez summarise the rule this way, and it applies to most field trials. If the direction of the gradient is unknown, compact square blocks are the safer choice. Within a block, the plots run along the gradient; this is consistent with the block lying across it. Border effects arise because outer rows of a plot compete less, or are damaged or shaded differently, compared with inner rows. Guard rows are sown around the net plot and are not harvested, and alleys between plots are kept equal. The net plot, not the gross plot, is used in the yield calculation.
The analysis of variance (ANOVA) partitions the total variation of the observations into parts attributable to identified sources (treatments, blocks, rows, columns) and a remainder, the error. Variation is measured by sums of squares of deviations. Each sum of squares has degrees of freedom; dividing a sum of squares by its degrees of freedom gives a mean square, which estimates a variance. If treatments have no effect, the treatment mean square and the error mean square both estimate the error variance, and their ratio F follows the F distribution with the treatment and error degrees of freedom. A large F, beyond the tabulated critical value at the chosen level of significance, leads to rejecting the null hypothesis that all treatment means are equal. Computation uses a correction factor CF = G squared / N, where G is the grand total and N the number of observations. The total sum of squares is the sum of all squared observations minus CF. The sum of squares for a classification is the sum over its groups of (group total squared / number of observations in the group), minus CF.
In a completely randomised design (CRD), treatments are allocated to all experimental units completely at random, with no blocking. Treatment i receives r_i units, and the total number of units is N, the sum of the r_i. Randomisation is simple: number the units from 1 to N and assign treatments using random numbers until each has its quota. The model is y_ij = mu + tau_i + e_ij, where mu is the general mean, tau_i the effect of treatment i and e_ij the independent random error with mean zero and constant variance. The ANOVA has three lines. Treatments: sum of squares = sum over i of (T_i squared / r_i) minus CF, with t - 1 degrees of freedom, where T_i is the total of treatment i. Error: obtained by subtraction, with N - t degrees of freedom. Total: N - 1 degrees of freedom. F = treatment mean square / error mean square. With equal replication r, the error degrees of freedom are t(r - 1). After a significant F, treatment means are compared. The standard error of a treatment mean is the square root of (MSE / r); the standard error of the difference between two means with equal replication is the square root of (2 MSE / r); with unequal replication it is the square root of MSE (1/r_i + 1/r_j). The critical difference (CD), also called the least significant difference, is t at the error degrees of freedom and chosen level multiplied by the standard error of the difference.
The CRD is the simplest design to lay out and analyse. It allows any number of treatments and unequal replication, which is useful when some units are lost or material is short. It leaves the maximum possible number of error degrees of freedom, and a missing observation causes no difficulty in the analysis, since the design simply becomes unequally replicated. Its weakness is that all variation between units, including systematic differences in soil or animals, goes into the error. The CRD is therefore efficient only when the experimental material is homogeneous: laboratory experiments, pot culture and greenhouse experiments where pots can be re-randomised, and animal trials with very uniform animals. In field experiments, where heterogeneity is almost always present, a CRD usually gives a larger error than a blocked design and is seldom used.
The coefficient of variation of an experiment is CV = (square root of MSE / grand mean) x 100, expressed as a per cent. It describes the experimental error relative to the mean and is used to judge the precision of a trial and to compare the precision of trials on the same crop and character. What counts as an acceptable CV depends on the crop, the character, the type of trial and the environment: characters such as days to flowering usually have small CVs and characters such as pest counts or yield under stress large ones. A CV much higher than usual for that kind of trial is a warning to check the data and the field management, not an automatic reason to discard the trial.
The randomised complete block design (RCBD, often called RBD) groups the experimental units into r blocks of t units each, such that units within a block are as alike as possible. Every treatment appears exactly once in every block, and the treatments are randomised separately and independently within each block. In a field, blocks are laid across the fertility gradient; in an animal trial, a block might be a litter, a weight class or a shed; in a laboratory, a batch or a day. Because each block is a complete replicate, the comparison between any two treatments is made within blocks, and the block-to-block variation drops out of treatment differences. The RCBD is the most widely used design in field research because it is simple, flexible in the number of treatments and replications, and effective whenever heterogeneity runs mainly in one direction.
The model is y_ij = mu + tau_i + beta_j + e_ij, with treatment effects tau_i, block effects beta_j and independent errors. The ANOVA has four lines. Blocks: sum over blocks of (B_j squared / t) minus CF, with r - 1 degrees of freedom. Treatments: sum over treatments of (T_i squared / r) minus CF, with t - 1 degrees of freedom. Error: by subtraction, with (r - 1)(t - 1) degrees of freedom. Total: rt - 1 degrees of freedom. The treatment F is the treatment mean square divided by the error mean square. The block mean square may also be compared with the error mean square to see whether blocking was useful, although blocks are not randomised and a formal test of blocks is not the purpose of the experiment. The standard error of a difference between two treatment means is the square root of (2 MSE / r) and the critical difference is t at (r - 1)(t - 1) degrees of freedom multiplied by it. The model assumes treatment and block effects are additive: a treatment raises yield by the same amount in every block. If treatments act multiplicatively, for example by a percentage, the additivity assumption fails and a log transformation may restore it (see the chapter on assumptions).
Compared with a CRD on the same units, the RCBD removes block variation from the error, at the cost of r - 1 error degrees of freedom. With t = 5 and r = 4, the CRD error has 15 degrees of freedom and the RCBD error 12. The design is efficient when blocks really differ, and the loss of degrees of freedom matters little unless the error degrees of freedom are already small. As the number of treatments grows, each block becomes larger and less homogeneous, and the advantage of blocking shrinks; with many entries, such as breeding trials with dozens or hundreds of lines, incomplete block designs (lattices, alpha designs, augmented designs) are preferred. A missing observation destroys the balance of an RCBD and must be handled by the missing-plot technique or by a general linear-model analysis. The RCBD controls one source of variation only; where heterogeneity runs in two directions, the Latin square or a row-column design is better.
A Latin square design (LSD) controls two sources of variation at once. With t treatments, the experimental area is divided into t rows and t columns, giving t squared plots, and the treatments are arranged so that each appears exactly once in every row and exactly once in every column. In a field, rows and columns can follow two fertility gradients at right angles; in animal or laboratory work, rows and columns can be two blocking factors such as animals and periods, or days and operators. Randomisation starts from a standard square (one whose first row and first column are in alphabetical order), chosen at random from the standard squares of that size where tables list them, and then the rows are randomised, the columns are randomised and the treatment letters are allocated to treatments at random. This keeps the Latin property while giving each layout a chance of being used.
The model is y_ijk = mu + rho_i + gamma_j + tau_k + e_ijk, with row, column and treatment effects. Row, column and treatment sums of squares are each computed as (sum of squared totals / t) minus CF, with t - 1 degrees of freedom each. The total has t squared - 1 degrees of freedom, so the error, found by subtraction, has t squared - 1 - 3(t - 1) = (t - 1)(t - 2) degrees of freedom. For a 4 x 4 square the error has only 6 degrees of freedom; for 5 x 5, 12; for 6 x 6, 20; for 8 x 8, 42. Few error degrees of freedom give an imprecise estimate of error and a large critical value, so small squares are weak unless they are repeated; large squares need many plots and the rows and columns become long and less homogeneous. In practice the Latin square is used for about four to eight treatments. The standard error of a difference and the critical difference are computed as in the RCBD with r = t.
The Latin square removes two sources of variation from the error and can therefore be much more precise than an RCBD when heterogeneity runs in two directions. Its limitations are that the number of replications must equal the number of treatments, that the analysis assumes no interaction between rows, columns and treatments, and that a missing plot or a wrongly treated plot complicates the analysis more than in simpler designs. A Graeco-Latin square superimposes two orthogonal Latin squares, one with Latin letters and one with Greek letters, so that every Latin letter occurs exactly once with every Greek letter. It can control three blocking factors or test two treatment factors in t squared units. Its ANOVA has rows, columns, Latin treatments and Greek treatments, each with t - 1 degrees of freedom, leaving (t - 1)(t - 3) degrees of freedom for error. Orthogonal Latin squares exist for every order except 2 and 6, so no Graeco-Latin square of order 6 exists; this is the answer to Euler's problem of the thirty-six officers.
The relative efficiency of design A compared with design B is the ratio of the error variances per unit that B and A would give on the same material, usually expressed as a per cent. A relative efficiency of 125% means that design B would need 1.25 times as many replications to give the same precision as design A. After an experiment has been run in one design, the error that a simpler design would have given can be estimated from the ANOVA, because the variation removed by blocking would otherwise have stayed in the error.
If an RCBD with r blocks and t treatments has block mean square Eb and error mean square Ee, the error mean square a CRD would have given on the same units is estimated as [(r - 1) Eb + r(t - 1) Ee] / (rt - 1). The relative efficiency of the RCBD over the CRD is therefore RE = [(r - 1) Eb + r(t - 1) Ee] / [(rt - 1) Ee]. When Eb equals Ee, blocking achieved nothing and RE is 1; the larger Eb is relative to Ee, the more blocking gained. When error degrees of freedom are fewer than about 20, the comparison is often adjusted for the different numbers of degrees of freedom by Fisher's factor (n1 + 1)(n2 + 3) / [(n2 + 1)(n1 + 3)], where n1 and n2 are the error degrees of freedom of the more and less refined design. Questions in this subject state whether that adjustment is to be applied.
A Latin square could have been laid out as an RCBD using either its rows or its columns as blocks. If the columns had been the blocks, the row variation would have gone into the error, and the estimated RCBD error mean square would be [Er + (t - 1) Ee] / t, where Er is the row mean square and Ee the Latin-square error mean square. The relative efficiency of the Latin square over that RCBD is RE = [Er + (t - 1) Ee] / (t Ee). The same formula with Ec, the column mean square, gives the efficiency relative to an RCBD with rows as blocks. These comparisons are used to decide whether to keep a two-way blocking in future trials on the same land: if the Latin square repeatedly shows high efficiency over both RCBD alternatives, heterogeneity runs in two directions; if one efficiency is near 100%, one blocking factor would have been enough.
Precision is the inverse of the variance of a treatment mean, r / sigma squared. A design can be made more precise by more replication, by a better design that reduces sigma squared, or by more uniform management and measurement. The CV is a scale-free summary of the error and lets different trials of the same character be compared. Choosing a design weighs the expected reduction in error against loss of error degrees of freedom, complexity, and the risk of missing plots. A practical sequence is: CRD for homogeneous material, RCBD for one-directional heterogeneity, Latin square for two-directional heterogeneity with few treatments, and incomplete block designs for many treatments.
Plots are lost to flooding, animal damage, theft, a sowing mistake or a sample spoiled in the laboratory. In a CRD this only creates unequal replication. In an RCBD or Latin square, however, the balance that makes the simple ANOVA formulae valid is broken: the treatment with the missing plot no longer appears in every block, and treatment totals are no longer comparable. The classical remedy, due to Yates (1933), is to estimate the missing value so that the error sum of squares of the completed data is as small as possible, insert it, and analyse the completed data in the usual way with one error degree of freedom subtracted for each value estimated. The estimated value is not an observation and adds no information; it simply lets the balanced formulae be used. Modern software instead fits the linear model to the observed data directly, which gives the same treatment estimates and exact tests.
If one plot is missing in an RCBD with t treatments and r blocks, let T be the total of the remaining plots of the treatment concerned, B the total of the remaining plots of the block concerned, and G the grand total of all observed plots. The estimate is x = (rT + tB - G) / [(r - 1)(t - 1)]. After inserting x, the error degrees of freedom are (r - 1)(t - 1) - 1 and the total degrees of freedom are reduced by one. The treatment sum of squares from the completed data is biased upward; the bias is [B - (t - 1) x] squared / [t (t - 1)], which is subtracted from the treatment sum of squares before F is calculated. The standard error of the difference between the mean of the treatment with the missing value and the mean of any other treatment is larger than usual: the square root of MSE [2/r + t / (r (r - 1)(t - 1))].
In a t x t Latin square, with R, C and T the totals of the observed plots in the row, column and treatment containing the missing plot and G the grand total of observed plots, the estimate is x = [t (R + C + T) - 2G] / [(t - 1)(t - 2)], and the error degrees of freedom fall by one. With two or more missing values, each estimate depends on the others. They can be found by solving the simultaneous equations that minimise the error sum of squares, or iteratively: guess all but one, estimate that one with the single-value formula, move to the next, and repeat until the values settle. One error degree of freedom is lost for each value estimated. The analysis of covariance, with a dummy covariate equal to 1 for a missing plot and 0 elsewhere, gives the same result and is another standard approach. When many plots are missing, or whole treatments in a block are lost, a general linear-model (least-squares) analysis of the observed data is the correct route.
The F test in the analysis of variance rests on four assumptions about the errors and the model: effects are additive (treatment, block and other effects add, without interaction between them in the designs of this subject); errors are independent; errors have a common variance in all treatments (homogeneity of variance, or homoscedasticity); and errors are normally distributed. Randomisation protects independence. The F test is fairly robust to moderate non-normality, especially with equal replication, but heterogeneous variances and non-additivity can distort both the F test and comparisons of means, particularly when replication is unequal. Typical agricultural failures are well known. Counts of insects, weeds or lesions follow distributions close to the Poisson, whose variance equals the mean, so treatments with high counts are more variable. Percentages derived from counts, such as germination or mortality, follow the binomial, whose variance p(1 - p)/n is smallest near 0% and 100% and largest near 50%. Yields across very different levels, or effects that act as percentages, often have standard deviations proportional to their means, and their treatment and block effects are multiplicative rather than additive.
Residuals (observed minus fitted values) are the main diagnostic. A plot of residuals against fitted values should show no pattern; a funnel shape indicates variance growing with the mean. A normal quantile plot of residuals checks normality. Homogeneity of variance across treatments can be tested by Bartlett's test, which is sensitive to non-normality, or Levene's test, which is less so. Additivity in a two-way classification without replication can be tested by Tukey's one-degree-of-freedom test for non-additivity. Outliers deserve investigation before any statistical remedy: a decimal-point error, a plot harvested twice or a damaged animal should be corrected from the field records, not transformed away.
When the variance depends on the mean in a known way, a transformation of the data can make variances nearly equal and often restores additivity too. The analysis is done on the transformed values and the results are reported as back-transformed means, while significance and critical differences refer to the transformed scale. Square-root transformation suits counts that follow the Poisson distribution, such as insects per plant or weeds per quadrat; when small values and zeros occur, the square root of (x + 0.5) is used. Logarithmic transformation suits data whose standard deviation is proportional to the mean or whose effects are multiplicative, such as numbers of insects over a wide range or growth data; log (x + 1) is used when zeros are present. The angular or arcsine transformation, angle = arcsine of the square root of p, suits binomial percentages derived from counts. Gomez and Gomez give a widely used rule for percentages: data lying between about 30% and 70% seldom need transformation; data lying wholly within 0-30% or within 70-100% may use the square-root transformation; data spread across a wider range use the arcsine transformation, with values of 0% and 100% replaced by 1/(4n) and 100 - 1/(4n) before transforming, where n is the number of units on which the percentage is based. Percentages that are not derived from counts, such as the percentage of protein in grain, are continuous measurements and are not given the arcsine transformation for that reason. Transformations are not a cure for every problem. When counts are sparse, proportions are extreme or variance patterns are complex, generalised linear models (Poisson, binomial or negative binomial) analyse the data on their natural scale and are now preferred by many statisticians.
A significant F says only that not all treatment means are equal. To find which differ, means are compared in pairs or as contrasts. With t treatments there are t(t - 1)/2 pairs: 10 for 5 treatments, 15 for 6, 45 for 10. If each pair is tested at 5%, the chance that at least one true null difference is declared significant (the experimentwise or familywise error rate) grows well above 5% as the number of comparisons rises. Multiple comparison procedures differ in how they balance this experimentwise error rate against the power to detect real differences. The most important choice is not between procedures but about the questions. Planned comparisons that follow from the treatment structure (a control against the rest, organic against inorganic sources, linear and quadratic trends for rates of a fertiliser) should be tested as orthogonal contrasts or regression components. Pairwise procedures suit unstructured sets of treatments such as varieties.
Fisher's least significant difference, LSD = t (alpha, error df) x square root of (2 MSE / r), is the critical difference used throughout this subject. Used only after a significant F (the protected LSD) and for a few planned comparisons, it is acceptable; used for all pairs among many treatments, it gives many false positives. Tukey's honestly significant difference, HSD = q (alpha; t, error df) x square root of (MSE / r), where q is the studentised range for t means, controls the experimentwise error rate for all pairwise comparisons. It is more conservative than the LSD. Note that the square root contains MSE / r, not 2 MSE / r, because the studentised range is defined on the standard error of a single mean. Duncan's multiple range test (DMRT) also uses studentised ranges, but the critical value depends on how many means lie between the two being compared when the means are ranked: means further apart in rank must differ by more. It was very widely used in agricultural journals; it controls neither the comparisonwise nor the experimentwise rate in a simple way and is less conservative than Tukey's test.
Dunnett's test compares each treatment with a single control, using critical values from Dunnett's tables that allow for the t - 1 comparisons being made with the same control mean. It is more powerful than Tukey's test for that limited question. The critical difference is d (Dunnett's tabulated value) x square root of (2 MSE / r). Scheffé's method allows any number of contrasts, including those suggested by the data after looking at them, while keeping the experimentwise error rate at alpha. A contrast is significant if its estimate exceeds the square root of [(t - 1) F (alpha; t - 1, error df)] multiplied by its standard error. It is the most conservative of the common procedures for pairwise comparisons, because it protects against a much larger family. The Bonferroni method tests each of m planned comparisons at level alpha / m, which keeps the experimentwise rate at or below alpha. It is simple and works for any type of test but becomes conservative when m is large.
Results are commonly shown as a table of means with the standard error of the mean, the CD (or HSD) and the CV, sometimes with letters: means sharing a letter do not differ significantly. Whatever the procedure, the report should name it, give the level of significance and the error degrees of freedom, and avoid testing all pairs when the experiment was designed around specific contrasts.
The analysis of covariance (ANCOVA) combines the analysis of variance with regression. It uses an auxiliary variable X, the covariate, measured on each experimental unit, to adjust the response Y for differences between units that blocking could not remove. Typical covariates are the initial body weight of animals in a feeding trial, the yield of the same plots in a uniformity trial or previous season, the pre-treatment count of pests in a spraying trial, and the number of plants established in a plot when stand differences are not caused by the treatments. The covariate must not be affected by the treatments. Initial weight is measured before feeding starts and is safe; plant stand measured after a seed treatment that changes emergence would remove part of the treatment effect, and adjusting for it would be wrong. The method also assumes a linear relation between Y and X, the same regression slope in every treatment, and a covariate measured with little error.
Sums of squares are computed for X and Y and sums of products for XY on every line of the ANOVA. Let Exx, Exy and Eyy be the error sums of squares and products. The within-treatment (error) regression coefficient is b = Exy / Exx. The error sum of squares of Y adjusted for X is Eyy - Exy squared / Exx, with one fewer degree of freedom than the unadjusted error, because one degree of freedom is used to estimate b. The adjusted treatment sum of squares is found by doing the same adjustment on the (treatment + error) line and subtracting the adjusted error, and F is formed from the adjusted mean squares. The adjusted mean of treatment i is the observed mean of Y minus b times the deviation of its covariate mean from the overall covariate mean: adjusted mean = mean Y_i - b (mean X_i - overall mean X). A treatment whose animals started heavier than average has its mean final weight adjusted downward. The error variance of differences between adjusted means includes an extra term for the uncertainty of b and the covariate difference, so adjusted means do not all have the same standard error.
Covariance analysis can estimate missing plots by including dummy covariates, can adjust for accidental damage measured on each plot, and in long-term experiments can use the previous yield of each plot to sharpen comparisons. Its efficiency gain over the unadjusted analysis grows with the correlation between Y and X within treatments. If that correlation is weak, the loss of one degree of freedom can make the adjusted analysis no better than the unadjusted one. Where a covariate is known before the trial, it can also be used to form blocks; blocking and covariance can be combined.
The number of replications needed depends on the size of difference the experimenter wants to detect, the error variance (or CV) expected from past trials on the same crop and land, the level of significance, and the power required, that is the probability of detecting the difference if it is real. Smaller differences, larger error, stricter significance levels and higher power all require more replications. Practical limits are land, uniform material, cost and management capacity: a trial with many replications that cannot be managed uniformly may end up less precise than a smaller trial run well.
For comparing two treatment means, the number of replications per treatment is approximately r = 2 (z_alpha + z_beta) squared sigma squared / d squared, where d is the difference to detect, sigma squared the error variance per unit, z_alpha the standard normal value for the chosen two-sided significance level (1.96 at 5%) and z_beta the standard normal value for the chosen power (0.84 for 80% power, 1.28 for 90%). If sigma and d are both expressed as percentages of the mean, the CV and the percentage difference can be used directly. The result is rounded up to the next whole number. Cochran and Cox give an exact version that uses t values at the error degrees of freedom and is solved iteratively, which gives slightly larger numbers for small experiments. Because the standard error of a difference is proportional to one over the square root of r, halving the detectable difference requires four times as many replications.
Precision also depends on how well the error variance is estimated. With very few error degrees of freedom the t and F critical values are large and the test has little power even if the true error is small. Many textbooks advise designing so that the error has at least about 10 to 12 degrees of freedom; in an RCBD with t treatments that means choosing r so that (r - 1)(t - 1) reaches that level. A single small Latin square, or an RCBD with few treatments and two replications, falls short of it. Replication in time and space is a separate decision. To recommend a variety or practice for a region, the experiment must be repeated over locations and seasons; extra replications at one site cannot substitute for this, because they do not sample the environmental variation over which the recommendation is meant to hold.
A student uses this subject twice: in examinations, where ANOVA tables, critical differences and missing-plot estimates are standard numerical questions, and in the thesis, where the first chapter of the methods section states the design, the experimental unit, the number of replications and how the treatments were randomised. Knowing the principles lets the student defend those choices at the viva and avoid the classic mistakes: counting sub-samples as replicates, laying blocks along a gradient, or testing every pair of means with an unprotected LSD.
A five-year scientist or station statistician designs dozens of trials a season with agronomists, breeders and animal scientists. The decisions are concrete: plot size given seed and machinery, block orientation given the slope and channel, RCBD or Latin square, how many replications for a 10% yield difference with the CV this station usually gets, whether initial weight should be a covariate, what to do with three plots lost to flooding, and whether the CV of this trial is acceptable. The same person writes the randomisation plans and checks the analyses that colleagues submit for publication.
A senior head of a statistics division sets the standards that make a research system's trials comparable: minimum replication and error degrees of freedom, required reporting of CV and the comparison procedure, rules for rejecting trials, and the use of uniformity-trial and historical data to plan layouts on each research farm. They decide when the institution moves from classical missing-plot and transformation techniques to mixed-model and generalised-linear-model analyses, and they train the people who analyse trials across many centres.
A PhD with twenty-five years builds on these foundations to develop new designs and analyses, teaches the subject and judges its correct use as a reviewer and examiner. Their work relies on the basic designs as reference points: optimality of block designs is defined against the RCBD, neighbour and spatial methods are judged by their efficiency over blocking, and the logic of randomisation underpins the inference they teach. They also preserve and reanalyse long-term and uniformity-trial data that show how field heterogeneity behaves.
This manual covers the basic designs and techniques. Factorial experiments, confounding, split- and strip-plot designs, incomplete block designs, response surfaces, groups of experiments, mixed-model and spatial analyses and generalised linear models are in other subjects of this track. Statistical tables are not reproduced: questions state the critical values they need. Derivations of expected mean squares and of the missing-plot formulas are outlined, not proved. What counts as an acceptable CV is deliberately not given as a single number because it depends on the crop, character and environment. The Latin-square missing-plot bias correction is omitted.
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 critical values needed are stated in the question.
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