Agricultural Statistics & Data Science · Design and analysis of experiments · also Cropping systems experimentation, Long-term experiments, On-farm research
The experiments that do not fit a textbook layout: intercropping and its indices, long-term fertiliser and cropping-system trials, animal and changeover feeding trials, repeated measures on the same plants or animals, on-farm and participatory trials, and sensory and laboratory experiments.
In the exams: AICE-JRF Agronomy Unit 6 'statistical analysis for cropping systems including intercropping' (heavy); AICE-JRF Ag Stat Unit 4 crossover designs (present); ASRB NET Ag Stat (reported)
Many agricultural experiments do not fit the textbook layout of treatments in uniform field plots measured once. This subject covers the experiments that need special designs or analyses: intercropping trials and their indices (LER, ATER and competition measures), cropping-system experiments and system equivalent yields, long-term experiments, repeated measures and growth curves, animal changeover and switchover designs with carry-over effects, livestock experiments where the pen is the unit, on-farm and participatory trials, experiments in orchards and perennial crops, pseudo-replication in laboratory, greenhouse and pot work, and sensory evaluation panels.
It draws on most of the other design subjects of this track: the experimental unit and pseudo-replication from the basic designs subject, crossover designs from the factorial subject, incomplete blocks for panels from the incomplete block designs subject, covariance structures and random effects from the mixed-models subject, and stability across farms and years from the multi-environment trials subject. Each chapter explains what is special about its kind of experiment and refers to those subjects for the general methods.
In examinations, the statistics unit of ICAR AICE-JRF/SRF Agronomy names methods of statistical analysis for cropping systems including intercropping, and AICE-JRF Agricultural Statistics Unit 4 names crossover designs. Typical questions ask for LER, ATER, aggressivity or equivalent yields, the experimental unit and error degrees of freedom in pen or chamber experiments, AUC or AUDPC, and the chance probabilities of sensory difference tests.
In intercropping, two or more crops grow together on the same land, as in maize with beans, sorghum with pigeonpea or coconut with cocoa. The yields of different crops cannot simply be added, and the yield of each crop in the mixture is naturally lower than its sole-crop yield because it occupies only part of the land or season. Intercropping experiments therefore include sole-crop plots of each component alongside the intercrop treatments, and the results are expressed through indices that compare intercrop yields with sole-crop yields.
The land equivalent ratio (LER), introduced by Willey and colleagues, is the relative land area under sole crops that would be needed to produce the yields achieved by intercropping: LER = sum over crops of Y_ij / Y_ii, where Y_ij is the yield of crop i in the intercrop and Y_ii its sole-crop yield. The terms Y_ij / Y_ii are the partial LERs. If maize yields 3.0 t/ha in the intercrop and 4.0 t/ha as a sole crop, and beans 0.6 t/ha intercropped and 1.2 t/ha sole, the partial LERs are 0.75 and 0.50 and the LER is 1.25: 25% more land would be needed to produce the same yields with sole crops. An LER above 1 indicates an intercropping advantage, below 1 a disadvantage. The choice of sole-crop yield in the denominator matters: using each block's sole yield introduces extra variability, using the mean sole yield over blocks is common, and using the best sole-crop yield (at its optimum density) gives a stricter, more conservative comparison. Because LER is a ratio, its statistical analysis should take care: it can be analysed by ANOVA when denominators are fixed (mean sole yields), but confidence intervals for ratios, or bivariate analyses of the two crops' yields, are more rigorous.
LER ignores the time each crop occupies the land. The area time equivalent ratio (ATER) of Hiebsch and McCollum weights each partial LER by the duration of the crop: ATER = sum of (Y_ij / Y_ii) t_i / T, where t_i is the duration of crop i and T the duration of the whole intercropping system. In the example, with maize lasting 120 days and beans 90 days in a 120-day system, ATER = (0.75 x 120 + 0.50 x 90) / 120 = 1.125, smaller than the LER because the short-duration beans could have been followed by another crop if grown alone. Competition indices describe how the crops interact. Aggressivity A_ab = Y_ab / (Y_aa Z_ab) - Y_ba / (Y_bb Z_ba), where Z_ab and Z_ba are the sown proportions; with 50:50 sowing in the example, A = 0.75/0.5 - 0.50/0.5 = 0.5, so maize is the dominant crop. The competitive ratio is the ratio of partial LERs adjusted for sown proportions, here 1.5. De Wit's relative crowding coefficient K_ab = Y_ab Z_ba / [(Y_aa - Y_ab) Z_ab] gives 3.0 for maize and 1.0 for beans; a product of the K values greater than one indicates a yield advantage. These indices are descriptive and should be reported alongside yields and LER, not as substitutes for them.
A typical intercropping experiment includes the sole crops of each component at their recommended densities, one or more intercrop arrangements (row ratios such as 1:1 or 2:1, or replacement versus additive series), and sometimes several densities. In a replacement series, one crop replaces the other in proportion, so total density is constant; in an additive series, the second crop is added to the full density of the first. The two series answer different questions and lead to different interpretations of competition indices. The sole crops should be grown in the same blocks as the intercrops so that LER denominators come from the same conditions.
Mead and Willey proposed the effective LER, which compares the intercrop with sole crops grown in the proportions needed to produce the same ratio of crop outputs, so that an intercrop is credited only for genuine yield advantage, not for producing an unusual mix of crops. Bivariate analysis of the two crops' yields, plotting intercrop treatments on axes of yield of crop A against yield of crop B and testing differences with bivariate methods (as developed by Pearce and Gilliver), avoids the ratio problems of LER and shows trade-offs between components directly.
Farmers judge intercrops by income and food, not only by land use. Monetary advantage (the value of the intercrop yields compared with the value of the better sole crop, scaled by LER) and gross returns per hectare complement LER. Where intercropping serves household nutrition, protein or energy outputs per hectare are compared. Reporting the components separately alongside such indices lets readers see where an apparent advantage comes from.
Each component's intercrop yield can be analysed by ANOVA over the intercrop treatments, but comparisons with its sole crop involve plots of different composition and often different variances, so separate error terms or weighted analyses may be needed. A common practical approach is to analyse partial LERs and total LER computed with block-mean sole yields as denominators, report standard errors, and support conclusions with the component yields themselves.
Cropping-system experiments compare sequences or combinations of crops over a year or several years, such as rice-wheat versus rice-maize versus rice-pulse rotations, often combined with nutrient, tillage or residue treatments. The experimental unit is a plot that carries the whole system over time, and treatments are the systems. Because the component crops differ, results are expressed on a common basis: the system yield equivalent, which converts each crop's yield into the equivalent yield of a base crop using prices, energy, protein or another common measure.
The rice-equivalent yield (REY) of a system is the sum over crops of yield times price divided by the price of rice. A rice-wheat system yielding 5 t/ha of rice priced at 20 per kg and 4 t/ha of wheat at 22 per kg has an REY of 5 + 4 x 22/20 = 9.4 t/ha. Price-based equivalents change with prices, so they should be reported with the prices used and, where possible, alongside energy- or protein-based equivalents. Other system measures include production efficiency (equivalent yield per day of system duration), land-use efficiency (the proportion of the year the land is cropped), net returns and benefit-cost ratios, and the sustainable yield index SYI = (mean yield - standard deviation) / maximum yield over years; with a mean of 4.0, a standard deviation of 0.6 and a maximum of 5.0 t/ha, SYI = 0.68. Statistically, system equivalent yields are analysed like any response, but year-to-year variation and correlation between years on the same plots must be considered (chapter 3), and component crops should also be analysed separately because a system total can hide opposite effects on different crops.
Price-based equivalents favour high-value crops and change from year to year, which can make a system look better or worse purely because of markets. Energy equivalents (calories per hectare) suit food-security comparisons, protein equivalents suit nutrition questions, and carbon or water-use equivalents suit environmental comparisons. A cropping-system report that gives two or three bases, and states the prices or conversion factors, lets readers judge robustness.
In rotation experiments, each phase of each rotation should ideally be present every year (all phases grown simultaneously on different plots), so that rotation effects are not confounded with year. If only one phase is grown each year, the comparison of rotations is confounded with the weather of the particular years in which each crop was grown. Analysis then needs care, and the experiment needs to run for at least one full cycle, preferably several, before rotations are compared.
Cropping-system experiments often need large plots because of machinery for several crops and because treatments such as tillage or residue management must be applied at field scale. Fewer, larger plots mean fewer error degrees of freedom; split-plot arrangements (systems in main plots, nutrient levels in sub-plots) are common, with the main-plot error used for system comparisons as explained in the factorial subject.
Some effects take decades to appear: soil organic matter changes slowly, nutrient deficiencies build up, weeds and diseases adapt, and yields under different managements may diverge only after many seasons. Long-term experiments, such as the Broadbalk wheat experiment at Rothamsted (begun in 1843) and many national long-term fertiliser and cropping-system experiments, are the only direct evidence on such effects. Their value grows with age, which is why they are maintained despite changes in varieties, methods and objectives.
Long-term experiments raise several difficulties. Treatments are fixed on the same plots, so observations over years on a plot are correlated; years are confounded with changes in varieties, management and climate; plots may have been modified during the experiment; and replication may be limited (some classical experiments are unreplicated). Analyses therefore include per-year ANOVAs to see how effects develop; regression of yield on time for each treatment, comparing slopes to test whether treatments diverge; mixed models with plots as subjects and temporal correlation (such as AR(1)) for the residuals, as described in the mixed-models subject; analyses of yield stability and sustainability indices over years; and, for unreplicated experiments, careful use of interactions with years or of spatial methods as error terms, with explicit caveats. Trends in treatment differences are usually more informative than trends in absolute yield, because absolute yields reflect variety changes and weather common to all treatments, whereas differences isolate the treatment effect.
Suppose in a long-term fertiliser experiment the yield of the unfertilised control declines by 20 kg/ha per year while the balanced-NPK treatment declines by only 5 kg/ha per year. The difference in slopes, 15 kg/ha per year, estimates how fast the benefit of balanced fertilisation grows; its standard error must account for correlation between successive years on the same plots, typically using a mixed model with an autoregressive structure. Regression of treatment differences on time is a simple robust alternative, provided the differences are approximately independent between years.
The scientific value of long-term experiments depends on records: what was applied, when varieties changed, which plots were modified, and how measurements were made. Archived soil and plant samples allow later re-analysis with new methods. Statisticians working with such experiments should document changes and include them in the analysis, for example as break points or covariates, rather than treating the series as homogeneous.
Some historic experiments have one plot per treatment. Their treatment differences can still be described, and sometimes tested using the treatment x year interaction or the variation among sections of plots as error, but these tests rest on assumptions (no persistent plot effects, independence between years) that should be stated plainly. Their main value is the long record itself, and conclusions are strongest when supported by replicated experiments elsewhere.
Many experiments record the same units repeatedly: plant height weekly, disease severity at several dates, animal weight monthly, soil moisture through a season. Analysing each date separately with its own ANOVA ignores the correlation between dates, multiplies the number of tests (inflating the chance of false positives), and does not answer the usual question, which concerns the pattern over time. Treating dates as a split-plot factor assumes compound symmetry, which rarely holds.
A simple and valid approach reduces each unit's profile to one or a few summary measures chosen for their biological meaning, then analyses those by ordinary ANOVA: the final value, the mean over dates, the slope of a fitted line, the time to reach a threshold, or the area under the curve (AUC). AUC by the trapezoidal rule is the sum over intervals of (time interval) x (average of the two adjacent values); with readings of 2, 6 and 8 at days 0, 10 and 20, AUC = 10 x (2 + 6)/2 + 10 x (6 + 8)/2 = 110. In plant pathology the same calculation for disease severity gives the area under the disease progress curve (AUDPC). Growth-curve models fit a curve to each unit's data (linear, polynomial, logistic or Gompertz, as developed in the crop forecasting and growth models subject) and compare the parameters among treatments, either in two stages or within a mixed model with random coefficients. Mixed models with covariance structures (AR(1), unstructured and others) model the whole data set directly and handle missing observations and unequal spacing. Profile analysis, a multivariate approach, tests parallelism and levels of treatment profiles when there are few time points and many subjects.
Disease severity on a plot is scored at 20%, 35% and 60% on days 40, 50 and 65 after sowing. The AUDPC is 10 x (20 + 35)/2 + 15 x (35 + 60)/2 = 275 + 712.5 = 987.5 percent-days. Each plot's AUDPC is then analysed by ANOVA like any plot response. Because intervals differ, the trapezoidal rule weights them correctly; a simple mean of the three scores would not. Relative AUDPC (divided by the maximum possible) allows comparison between seasons with different numbers of assessments.
Summary measures are simple and robust and should be chosen before seeing the data. Mixed models are more efficient and handle missing values but require choices about covariance structures. When treatments are expected to change the shape of growth (for example, a growth regulator that delays early growth but not final size), comparing growth-curve parameters such as the asymptote, rate and inflection time answers the biological question better than comparing values at individual dates.
When measurements are at fixed, few dates, time can be treated as a factor with covariance structures among dates. When measurements are many or irregular, treating time as a continuous covariate in a growth-curve or random-regression model is more natural and more parsimonious. Either way, treatment x time interaction is usually the effect of interest, because it shows how treatment effects develop.
Plants die, animals are culled and readings are missed. Summary-measure approaches need a rule for incomplete profiles (for example AUC over the available interval, or exclusion with reporting), whereas likelihood-based mixed models use all available data and remain valid if values are missing at random. The reason for missingness should always be recorded, because dropouts related to treatment (deaths from a toxic diet) are themselves results.
The factorial subject introduced crossover (changeover) designs, in which each animal receives a sequence of treatments in successive periods, with Latin squares as the standard layout and Williams designs to balance first-order carry-over. In animal nutrition and veterinary trials several further designs are used. Extra-period designs (Lucas) repeat the last treatment of each sequence in an additional period, which makes direct and carry-over effects orthogonal and estimates carry-over efficiently. Switchback or reversal designs (A-B-A, B-A-B), associated with Brandt and Lucas, compare treatments against a trend within the lactation. Double reversal designs extend this to more periods.
Carry-over (residual) effects arise when a treatment's effect persists into the next period: a high-energy ration may raise body condition that supports milk yield in the following period, or a drug may remain in tissues. Defences are washout periods between treatments, discarding the first part of each period as an adaptation phase, designs balanced for carry-over, and models that estimate direct and residual effects explicitly. If carry-over is large and unequal between treatments, only first-period data are free of it, and the trial reduces to a parallel-group comparison with fewer animals. A preliminary (standardisation) period before treatments begin provides covariate data that can sharpen comparisons.
With two rations A and B in a two-period crossover, the sequences AB and BA cannot separate carry-over from the treatment x period interaction. Adding a third period that repeats the second treatment (sequences ABB and BAA) gives Lucas's extra-period design, in which each treatment follows itself and the other treatment, allowing direct and carry-over effects to be estimated separately and efficiently. The cost is one more period per animal, which in lactation trials must fit within the stable part of the lactation.
Crossover designs are efficient only when treatments have no lasting effects and animals return to a similar state between periods. Treatments that permanently change the animal (vaccination, growth-stage effects, reproductive treatments), long-term responses such as growth over months, and diseases that are cured or kill the animal require parallel-group designs, with each animal receiving one treatment, usually with blocking by initial weight, parity or litter and with covariance on pre-trial measurements.
Milk yield or feed intake measured during a standardisation period before treatments begin is a powerful covariate for comparisons in parallel-group trials and can also be used in changeover designs. Its value depends on the correlation between pre-trial and trial measurements; adjusting for it is especially worthwhile when animals differ greatly in level of production, as they usually do.
Changeover designs reduce the number of animals needed because each serves as its own control, which is important for animal welfare and cost. The number of periods is limited by the stable part of the production cycle (for dairy cows, mid-lactation) and by the length of each period needed for adaptation and measurement. Typical nutrition trials use three or four periods of three to five weeks, with the first one to two weeks of each period treated as adaptation.
In many livestock experiments, animals are kept and fed in groups: broilers in pens, pigs in pens, fish in tanks, calves in group housing. If a feed treatment is applied to the pen, the pen is the experimental unit, and the animals within it are sub-samples, exactly as plants within a pot in the basic designs subject. Feed intake and feed conversion ratio (FCR, feed consumed divided by weight gain) are measured per pen, and treatment comparisons must use the variation between pens receiving the same treatment, not between animals. Analysing individual birds as replicates is pseudo-replication and exaggerates precision.
The number of error degrees of freedom depends on the number of pens, not the number of animals: four diets with three pens each in a CRD have 12 - 4 = 8 error degrees of freedom whether each pen holds 10 or 100 birds. More animals per pen improve the precision of each pen mean, but with diminishing returns once pen-to-pen variation dominates; more pens per treatment are usually the better investment. Pens are often blocked by location in the house (near the fan or door, upper or lower tier of cages), and initial weight per pen can serve as a covariate. Individual-animal measurements such as carcass traits can be analysed with a mixed model that has pens as a random effect, which correctly separates between-pen and within-pen variation. Mortality during the trial changes the number of animals per pen and the feed eaten by animals that later died; FCR is usually corrected for the weight of dead birds, and the correction method should be stated.
Suppose a broiler trial compares four diets. Design A uses two pens per diet with 50 birds each; design B uses five pens per diet with 20 birds each, the same 400 birds. Design A has 8 - 4 = 4 error degrees of freedom; design B has 20 - 4 = 16. If the variance between pen means is dominated by pen effects (house position, feeder function) rather than by bird-to-bird variation, design B gives far more precise and reliable comparisons, and its F and t critical values are much smaller. Reviewers of feeding trials increasingly insist on adequate numbers of pens.
When animals are fed individually (individual pens or electronic feeders that record each animal's intake), the animal becomes the experimental unit for feed responses, but animals housed together may still influence each other through competition or disease. Electronic feeding systems in group housing allow individual intake records while keeping social conditions realistic; the analysis then often includes the group as a random effect to capture shared conditions.
Reports should state the experimental unit, the number of units per treatment, the number of animals per unit, how mortality and culls were handled, and the model used, including any random pen or block effects. Statements such as 'n = 400 birds' without the number of pens make it impossible for readers to judge the validity of the tests.
On-farm trials test technologies under farmers' conditions, where results matter most. They range from researcher-designed and researcher-managed trials on farmers' fields (close to station trials in control), through researcher-designed farmer-managed trials (testing performance under farmers' management), to farmer-designed and farmer-managed trials (testing what farmers themselves choose and how they adapt it). Each farm usually acts as a block or replicate, with few treatments per farm, and many farms provide the replication. The variation among farms is a source of information about how widely a technology works, not only a nuisance.
In the mother-baby design (Snapp and colleagues), a researcher-managed 'mother' trial with all treatments and replication is located centrally in a village, and farmer-managed 'baby' trials on surrounding farms each test a subset of treatments, often one or two against the farmer's practice. Mother trials give precise comparisons; baby trials give realistic performance and farmer evaluation. Participatory variety selection lets farmers rank or score varieties; rankings are analysed with non-parametric methods (Friedman's test for complete rankings) or models for paired and ranked comparisons (Bradley-Terry and Plackett-Luce models). The triadic comparison approach (tricot), in which each farmer tests three of many varieties and ranks them, uses incomplete-block ideas at very large scale. Analysis of on-farm trials with mixed models treats farms as random, estimates the farm x treatment interaction, and can relate it to farm characteristics such as soil type or planting date. Missing data, unequal management and farmers' changes to protocols are common and should be recorded rather than hidden.
In a participatory trial, 40 farmers each rank four varieties from best (1) to worst (4). Friedman's test compares the rank sums of the varieties, treating farmers as blocks. If each farmer tests only three of ten varieties, as in tricot, the data are incomplete rankings, and models such as Plackett-Luce estimate a worth parameter for each variety from all the partial rankings, with covariates such as farmer gender or location explaining preference differences. Such analyses combine farmers' knowledge with statistical inference at a scale that researcher-managed trials cannot reach.
In a set of on-farm trials, the treatment effect usually varies between farms. Estimating that variation, as a random farm x treatment component, tells how often a technology will pay on a given farm, which matters more to farmers than the average effect. Relating the interaction to farm characteristics (soil fertility, rainfall, planting date, management level) supports targeted recommendations, in the same spirit as the multi-environment trials subject.
On-farm data have more measurement problems than station data: plot sizes may be approximate, harvest weights estimated, and management dates uncertain. Simple checks (plausible ranges, consistency with neighbouring farms, photographs of plots and harvests) and recording of what actually happened on each farm improve analyses. Farms where protocols were not followed can be analysed with an indicator variable rather than dropped silently.
Because farm-to-farm variation in treatment effects is usually large, on-farm programmes need many farms to estimate average effects and their variability well; tens of farms per region are common in variety and practice testing, and tricot-style programmes involve hundreds or thousands of farmers. Fewer treatments per farm keep the burden on each farmer manageable, and incomplete-block thinking ensures that all treatments are still compared across the network.
Experiments with fruit trees, plantation crops and other perennials differ from annual crop trials in several ways. The unit is often a single tree or a small group of trees, and trees differ greatly in vigour and yield even under the same treatment, so experimental error is large. Trees occupy land for many years, limiting the number of units; treatments may take years to show effects; and responses carry over between years, as with alternate bearing. Guard trees separate treated units to avoid interference through roots, shading or spray drift.
The most effective tool is covariance analysis using pre-treatment measurements on each tree: yield in previous years, trunk girth or cross-sectional area, or canopy volume, as described in the basic designs subject. These covariates can remove much of the tree-to-tree variation and are usually more effective than blocking alone, although blocking by position or by covariate classes is also used. Uniformity data from the first years of an orchard serve the same purpose as uniformity trials in field crops. Repeated annual yields should be analysed with methods for correlated data (chapter 4 and the multi-environment trials subject), and cumulative yield over years gives a robust overall comparison. Single-tree plots with many replicates are often more efficient than multi-tree plots with few replicates, provided interference between neighbouring trees is controlled.
In a fertiliser trial on mango, pre-treatment yields of individual trees vary from 40 to 160 kg. If the within-treatment regression of treatment-year yield on pre-treatment yield is strong (say a correlation of 0.7), covariance analysis reduces the error variance to roughly 1 - 0.7 squared = 51% of its unadjusted value, nearly halving the number of trees needed for the same precision. The pre-treatment yields must be recorded before treatments start, so that they cannot be affected by the treatments.
Root systems and canopies extend beyond the space allotted to each tree, so a fertilised tree may benefit an unfertilised neighbour, and spray drift or shading may cross plot boundaries. Guard rows, adequate spacing between treated units, and designs that place treatments so that neighbours are balanced reduce bias. In trials of rootstocks or training systems, where tree size differs between treatments, interference can be large and must be considered in the design.
Perennial trials outlast staff and sometimes institutional priorities. Clear protocols, documented randomisation, permanent plot maps and archived data protect the investment. Intermediate analyses (for example after the first fruiting years) should be planned in advance, recognising that early results may not predict long-term performance, especially when alternate bearing or slow establishment are involved.
Hurlbert (1984) defined pseudo-replication as the use of inferential statistics to test treatment effects with data from experiments where treatments are not replicated (though samples may be) or replicates are not statistically independent. Typical examples in agricultural research: each temperature applied in one growth chamber with many pots inside, so chamber and temperature are confounded; a single tank per feed with many fish; one field plot per treatment sampled at many points; or measurements on several leaves of the same plant treated as replicates. In all these cases the samples share the same application of the treatment and the same unit-level disturbances, and the variation among them does not estimate the experimental error relevant to treatment comparisons.
The remedies are design remedies: replicate the units to which treatments are applied (several chambers per temperature, or repeat the experiment over time with re-randomised chamber assignments), apply treatments independently to each replicate, and analyse with the correct unit, averaging sub-samples or using a mixed model with sub-samples nested in units. When only one chamber per treatment is possible, repeating the experiment in several runs with treatments re-assigned to chambers makes runs the replicates. Greenhouse benches and growth rooms also have gradients in light, temperature and humidity, so pots should be blocked by position or re-randomised (rotated) regularly, and edge effects avoided with guard pots. Laboratory assays have batch and day effects that call for blocking by batch. Where the unit is truly homogeneous and treatments are applied to each pot independently, a CRD with pots as units is valid.
A study of temperature effects with three temperatures and only three growth chambers cannot separate temperature from chamber. Running the experiment three times, each time assigning temperatures to chambers at random, gives three replicates per temperature with chamber effects randomised across runs; the analysis treats run as a block and run x chamber combinations as the experimental units. Measurements on the pots within a chamber in a run are averaged or treated as sub-samples. The extra time is the price of a valid test.
Light and temperature gradients from vents, walls, heating pipes and shading structures can be substantial on greenhouse benches. Laying out pots in randomised blocks along the gradient, rotating pot positions at intervals (with the rotation scheme recorded), and excluding edge positions or using them for guard plants all reduce bias. Uniformity data from a blank run of plants can show the pattern of variation in a particular greenhouse, as uniformity trials do for fields.
In laboratory work, technical replicates (repeated measurements of the same extract or sample) assess measurement precision, while biological replicates (independent samples from independently treated units) assess treatment effects. Only biological replicates justify inference about treatments. Reports should state both numbers; three technical replicates of one biological sample per treatment amount to an unreplicated experiment.
In microbiology and seed testing, dishes in one incubator share temperature and humidity; if treatments are applied to dishes independently, dishes are units, but if a treatment is the incubator condition, incubators (or runs) are the units. Germination tests use replicates of seeds (for example four replicates of 100 seeds) as the units, not individual seeds, and the standard procedures of seed-testing rules specify tolerances between replicates.
Sensory evaluation of foods, beverages and agricultural products uses human assessors, who differ in sensitivity, use of scales and mood. Assessors are treated as blocks (or as random effects) so that treatment comparisons are made within assessors. Samples are presented in balanced orders to control order and carry-over effects (a strong-flavoured sample affects the next), using designs balanced for first-order carry-over such as Williams Latin squares. When an assessor cannot taste all samples without fatigue, balanced incomplete block designs, as in the incomplete block designs subject, assign subsets of samples to each assessor.
Affective (consumer) tests measure liking, commonly with the 9-point hedonic scale, and are analysed by ANOVA with assessors as blocks or by non-parametric methods; ranking tests use Friedman's test. Discrimination tests ask whether assessors can detect a difference at all. In the triangle test, each assessor receives three samples, two alike and one different, and must identify the odd one; under the null hypothesis of no detectable difference the probability of a correct answer is 1/3. In the duo-trio and paired-comparison tests the chance probability is 1/2. Significance is assessed with the binomial distribution or its normal approximation: with 30 assessors in a triangle test, the expected number correct under the null is 10 with standard deviation the square root of (30 x 1/3 x 2/3) = 2.58, so 15 correct gives z = (15 - 10)/2.58 = 1.94, significant at the 5% level (one-sided). Descriptive analysis with trained panels rates intensities of attributes such as sweetness or firmness on line scales; panel performance (agreement, repeatability and discrimination of each assessor) should be checked, and multivariate methods (principal component analysis) summarise the attribute profiles. Sensory data feed directly into product development and into quality evaluation of new varieties and processing methods.
Before a descriptive panel's data are used, each assessor's performance is checked: discrimination (does the assessor distinguish samples that differ?), repeatability (similar scores for replicate samples) and agreement with the panel (similar ranking of samples). Mixed models with assessor and assessor x sample terms quantify these, and poorly performing assessors are retrained. Scaling differences between assessors (some use the full scale, others a narrow range) are common and are partly handled by treating assessors as blocks or random effects.
Consumer acceptance tests need many more assessors than trained-panel tests, because consumers vary widely in preference; numbers in the order of 60 to 100 or more are common in practice. Discrimination tests are planned with power calculations based on the binomial distribution: the number of assessors needed depends on the proportion of the population expected to detect the difference and on the chosen error rates. Presentation order, serving temperature, coding of samples with random three-digit numbers and palate cleansing between samples are standard controls.
The 9-point hedonic scale is ordinal, though it is commonly analysed by ANOVA as if interval-scaled; this is usually acceptable with many assessors and moderate scores but can mislead near the scale ends. Ordinal (proportional odds) models are an alternative that respects the scale. Whatever the method, assessors should be a relevant population of consumers, not only laboratory staff, if conclusions about consumer acceptance are intended.
In a paired preference test each consumer states which of two samples they prefer. Under the null hypothesis of no preference the probability of choosing either is one half, and the test is two-sided because either sample could be preferred. This differs from the one-sided paired difference test, in which assessors identify the sample with more of a stated attribute and only correct identifications count.
Students in agronomy, animal science, horticulture and food technology run exactly these experiments in their theses: intercrops, rotations, feeding trials in pens, pot and growth-chamber studies, orchard trials and sensory panels. They must identify the experimental unit, choose a design that avoids pseudo-replication, and analyse indices, repeated measurements and panel data correctly.
A five-year station statistician advises on all of these: how many pens per diet, how to analyse weekly growth data, whether a growth-chamber study is replicated, how to set up mother-baby trials, how to use pre-treatment yields in an orchard trial, and how to design a tasting panel. Much of the work is catching design errors before trials start.
A senior statistician sets institutional standards for experimental units in animal and greenhouse research, maintains long-term experiments and their data, and designs large on-farm and participatory programmes. They advise ethics and funding committees on whether proposed animal experiments use the minimum number of animals consistent with valid conclusions.
A PhD with long experience develops methods for these settings (analysis of long-term experiments, models for ranked participatory data, designs balanced for carry-over, indices for intercropping), teaches them, and reviews research for design validity.
Formulas for competition indices are given in their common forms; several variants exist in the literature. Detailed models for ranked data (Bradley-Terry, Plackett-Luce), profile analysis and Lucas's extra-period designs are described, not derived. Specific numbers (prices, sole-crop yields, panel sizes) in examples are illustrative. Animal welfare regulations governing experiment sizes differ by country and are not covered.
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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