Agricultural Statistics & Data Science · Statistical genetics and biometrics · also Biological Assay, Survival Analysis, Statistical Methods in Epidemiology
Dose and response, time to event and disease in populations: direct and indirect assays, probit and logit analysis of LD50 and LC50, parallel-line and slope-ratio assays, Kaplan-Meier and Cox models, and the statistical side of plant and animal epidemiology. Introductory veterinary epidemiology lives in the Veterinary track; this is the statistics behind it.
In the exams: Light in AICE-JRF Ag Stat; ICAR MSc/PhD elective; plant-protection and veterinary research (applied); UPSC ISS (light)
This subject brings together three bodies of statistical method that plant-protection, veterinary and public-health scientists use every day. Biological assay (bioassay) measures the potency of a pesticide, drug, vaccine, vitamin or biocontrol agent by its effect on living organisms, comparing a test preparation with a standard. Survival analysis studies times to an event, such as death of an insect after exposure, failure of a seed to remain viable in storage, onset of disease in an animal, or time to adoption of a practice, when many times are incompletely observed. Epidemiological statistics measures disease frequency and its association with exposures in populations of plants and animals, evaluates diagnostic tests, and describes how epidemics progress in the field.
The statistical tools come from earlier subjects, which this manual cites rather than repeating: the binomial and exponential-family models and generalized linear models (Categorical Data Analysis and GLMs, which already covers logistic and probit regression, LD50 estimation in outline and odds ratios in contingency tables), maximum likelihood and its asymptotic theory (Statistical Inference I), likelihood-ratio and score tests (Statistical Inference II), and Poisson processes and hazard ideas (Probability Theory and Stochastic Processes). What is new here is the structure of the applied problems: relative potency and its confidence limits, censored data, hazard-based models, the logic of epidemiological study designs, and the measurement of disease in crops over time.
The chapters cover direct and indirect assays; quantal-response analysis by probits and logits; parallel-line and slope-ratio assays with Fieller's theorem; censoring and truncation; the Kaplan-Meier estimator and log-rank test; the Cox proportional hazards model; exponential and Weibull survival models; measures of disease frequency and association; cohort, case-control and cross-sectional designs; diagnostic-test evaluation; and disease progress curves with the area under the disease progress curve (AUDPC). Introductory veterinary epidemiology is taught in the Veterinary track; this subject supplies the statistics behind it.
The subject is examined lightly in the ICAR AICE-JRF Agricultural Statistics paper and the Indian Statistical Service, and it is an MSc and PhD elective at agricultural universities; its weight in practice is much greater, in insecticide-resistance monitoring, efficacy trials of pesticides and seed treatments, vaccine potency testing, livestock disease surveillance and plant-disease epidemiology.
A biological assay estimates the potency of a test preparation T relative to a standard preparation S of the same active principle, from the responses of living subjects. The central quantity is the relative potency ρ: the number of units of S equivalent in effect to one unit of T. The fundamental assumption is that T behaves as a dilution (or concentration) of S, so that a dose z of T acts exactly like a dose ρz of S; assays satisfying this are analytical dilution assays, and the assumption must be checked, because a test preparation containing a different active compound may not behave as a dilution at all.
Assays are classified by how the response is observed. In a direct assay the dose needed to produce a fixed response (death, a specified reaction) is measured on each subject, by increasing the dose until the response occurs; each subject yields its own tolerance. In an indirect assay, fixed doses are given to groups of subjects and the response is recorded: a quantitative (graded) response such as weight gain or growth inhibition, or a quantal (all-or-none) response such as death or survival. Most pesticide and vaccine assays are indirect.
In a direct assay with tolerances observed on nₛ subjects for the standard and n_T for the test, the relative potency is estimated by the ratio of mean tolerances, ρ̂ = z̄ₛ/z̄_T, because one unit of T needs ρ units of S. Tolerances are often log-normally distributed, in which case analysis on the log scale is preferable: log ρ̂ = mean(log zₛ) − mean(log z_T), with a confidence interval from the two-sample t distribution, back-transformed. When the analysis is on the original scale, confidence limits for the ratio of means come from Fieller's theorem (Chapter 3).
Example: the doses of a standard insecticide solution needed to kill 6 insects, fed continuously until death, average 2.4 μg, and those of a new formulation average 1.6 μg. Then ρ̂ = 2.4/1.6 = 1.5: one microgram of the new formulation is as effective as 1.5 μg of the standard. Direct assays are rare in agriculture because doses can seldom be increased continuously until a response occurs on the same organism; the classic examples are pharmacological (digitalis infused into animals until heart arrest). Their logic, however, underlies every indirect assay: the potency ratio is a horizontal shift between dose-response curves of identical shape.
In a quantal assay, groups of nᵢ subjects receive dose zᵢ (usually on a log scale, xᵢ = log zᵢ) and rᵢ respond. If each subject's log tolerance is normally distributed with mean μ and standard deviation σ, the proportion responding at log dose x is P(x) = Φ((x − μ)/σ), so Φ⁻¹(P) = (x − μ)/σ is linear in x. Bliss and Finney's probit analysis worked with probits, Φ⁻¹(P) + 5 (the 5 avoided negative numbers in hand calculation), and fitted the line by iterative weighted least squares (maximum likelihood), which is exactly the binomial GLM with probit link of the categorical-data subject. The logit model, logit P = α + βx, from a logistic tolerance distribution, gives nearly identical fits in the central range and differs mainly in the tails.
The median lethal dose LD50 (or lethal concentration LC50, effective dose ED50) is the dose at which half the subjects respond: on the log scale log LD50 = μ = −α/β for the fitted line α + βx. Other quantiles follow: log LD90 = (Φ⁻¹(0.9) − α)/β for the probit, (log 9 − α)/β for the logit. The slope β = 1/σ measures how homogeneous the population's tolerances are; resistance monitoring tracks both LD50 shifts and slope changes. Resistance ratios are LD50 (field population)/LD50 (susceptible strain).
Steps in a typical analysis: correct for control mortality c by Abbott's formula, P_corrected = (P − c)/(1 − c), or estimate c as a parameter; fit the probit or logit line by maximum likelihood; check goodness of fit with the heterogeneity chi-square Σ(rᵢ − nᵢP̂ᵢ)²/[nᵢP̂ᵢ(1 − P̂ᵢ)] on k − 2 degrees of freedom (k doses); if it is significant, inflate variances by the heterogeneity factor χ²/(k − 2) and use t instead of z for limits; and compute LD50 with fiducial (Fieller) limits.
Example: a logit fit gives logit P = −4.6 + 2.3 log₁₀(dose in mg/L). Then log₁₀ LC50 = 4.6/2.3 = 2.0 and LC50 = 100 mg/L; the LC90 has log dose (2.197 + 4.6)/2.3 = 2.955, i.e. 902 mg/L.
Non-parametric alternatives estimate the LD50 without assuming a tolerance distribution. The Spearman-Kärber method, for equally spaced log doses with response proportions rising from 0 to 1, gives log LD50 = x_k + d/2 − dΣpᵢ, where x_k is the highest log dose, d the spacing and pᵢ the observed proportions (summed over all doses), and its trimmed version handles curves that do not reach 0 and 1. Such methods are robust but give no slope and no extrapolation to other quantiles. Designing a quantal assay means choosing doses that bracket the expected LD50 with responses between about 10% and 90%, since doses giving 0% or 100% response carry little information about the line.
In a parallel-line assay the mean response is linear in log dose for both preparations: y = αₛ + βx for the standard and y = α_T + βx for the test, with a common slope. Since dose z of T acts like dose ρz of S, the test line is the standard line shifted horizontally by log ρ: α_T = αₛ + β log ρ, so log ρ = (α_T − αₛ)/β, estimated as M = (ȳ_T − ȳₛ)/b − (x̄_T − x̄ₛ), with b the common slope estimated from the pooled within-preparation regression. Quantal assays analysed with probits or logits on log dose are parallel-line assays in the same sense.
The analysis of variance for a balanced design (for example a (3, 3) assay with three log-equally-spaced doses of each preparation) partitions the dose sum of squares into preparations, regression, parallelism (difference in slopes), and deviations from linearity (quadratic and higher terms). A valid assay needs a significant regression, non-significant departure from parallelism and non-significant departure from linearity; a significant preparations term is expected whenever the potencies differ. Non-parallel lines mean that the test does not behave as a dilution of the standard, so no single relative potency exists. Pharmacopoeial and regulatory standards prescribe such validity checks; their exact requirements vary by country and product.
In a slope-ratio assay the response is linear in dose itself (not log dose), as in many microbiological assays of vitamins and amino acids: y = α + βₛz for the standard and y = α + β_Tz for the test, with a common intercept (zero dose gives the same response whichever preparation is 'given'). Since z of T acts like ρz of S, β_T = ρβₛ and ρ = β_T/βₛ, a ratio of slopes. Validity checks are a common intercept (often tested by including a blank, zero-dose group) and linearity.
Relative potency is always a ratio (or a difference on the log scale divided by a slope), so its confidence limits come from Fieller's theorem. For a ratio m = a/b of normally distributed estimates with variances v₁₁, v₂₂ and covariance v₁₂ (in units of an error variance), define g = t²v₂₂/b². The limits are [m − gv₁₂/v₂₂ ± (t/b)√(v₁₁ − 2mv₁₂ + m²v₂₂ − g(v₁₁ − v₁₂²/v₂₂))]/(1 − g). When g is small (below about 0.05 to 0.1) the limits are close to the delta-method interval m ± t√(v₁₁ − 2mv₁₂ + m²v₂₂)/b; as g approaches 1 the interval becomes very wide and asymmetric, and for g ≥ 1 it is unbounded, signalling that the slope is not significantly different from zero and the potency cannot be estimated. In parallel-line assays with log doses, Fieller limits for log ρ are back-transformed to limits for ρ.
Example of the size of g: with a slope estimate b = 2.0, standard error 0.4 and t = 2.0, g = 4 × 0.16/4 = 0.16, large enough that Fieller limits differ noticeably from symmetric delta-method limits.
Survival analysis studies a non-negative time T to an event. Its distribution is described by the survival function S(t) = P(T > t); the hazard function h(t) = f(t)/S(t), the instantaneous event rate among those still at risk; and the cumulative hazard H(t) = ∫₀ᵗh(u)du, with S(t) = exp[−H(t)]. A constant hazard gives the exponential distribution; increasing hazards describe wear-out and ageing, decreasing hazards early failure and selective survival of the robust.
The defining feature of survival data is censoring: for some subjects the event time is known only partly. Right censoring is the usual case: a subject is followed until time c without the event, so T > c. In Type I censoring the study ends at a fixed time (insects observed for 7 days; seeds stored for 12 months), so all survivors are censored at the same time. In Type II censoring the study ends after a fixed number of events. Random censoring arises when subjects leave the study for unrelated reasons (an animal is sold, a plot is lost). Left censoring means the event happened before observation began (an infection already present at the first test), and interval censoring means the event is known only to lie between two inspection times, as with periodic germination or disease checks.
Ignoring censoring is a serious error. Dropping censored subjects discards the information that they survived at least to c and biases survival estimates downward; treating censoring times as event times does the same. Methods for survival data use each subject's contribution to the likelihood correctly: f(tᵢ) for an observed event and S(cᵢ) for a right-censored time, which is why the exponential MLE is the number of events divided by total time at risk (Chapter 7). The key assumption is non-informative (independent) censoring: subjects censored at time c must have the same future risk as those still under observation. Animals removed from a trial because they look ill violate it.
Truncation differs from censoring: subjects whose event times fall outside a window are not observed at all. Left truncation (delayed entry) occurs when subjects enter observation only after some time has passed, for example trees entered in a study only if they were alive when surveyed; they must be counted in the risk set only from their entry time. Ignoring left truncation overestimates survival, because short-lived individuals were never seen. Agricultural examples of survival data include time to death of insects after exposure, time to germination (with seeds that never germinate censored at the end of the test), seed longevity in storage, time to first disease symptoms, time to culling of dairy cows, and time to adoption of a technology after its release.
Germination tests illustrate the point well. Seeds are checked daily for 14 days; a seed germinating on day 5 gives an event time of 5 (strictly, an interval between days 4 and 5), and a seed that has not germinated by day 14 is right-censored at 14, not 'failed'. Reporting only the final germination percentage and a mean germination time computed from germinated seeds alone mixes two different questions, how many seeds germinate and how fast, and the mean time is biased if slow germinators are cut off at day 14. Survival methods (Kaplan-Meier curves of time to germination, or cure models that allow a fraction never to germinate) answer both questions together.
The Kaplan-Meier (product-limit) estimator of the survival function, from right-censored data, is Ŝ(t) = Π over event times tⱼ ≤ t of (1 − dⱼ/nⱼ), where dⱼ is the number of events at tⱼ and nⱼ the number at risk just before tⱼ (subjects who have neither had the event nor been censored). Censored subjects contribute to the risk sets up to their censoring time and then leave. The estimate is a step function dropping only at event times; with no censoring it reduces to the empirical survival function. Greenwood's formula estimates its variance: Var[Ŝ(t)] ≈ Ŝ(t)² Σ dⱼ/[nⱼ(nⱼ − dⱼ)], and confidence intervals are better computed on the log(−log) scale to stay within [0, 1]. The median survival time is the smallest t with Ŝ(t) ≤ 0.5. The Nelson-Aalen estimator Ĥ(t) = Σ dⱼ/nⱼ estimates the cumulative hazard.
Example: 10 insects are exposed; deaths occur at days 2, 3, 3 and 5, one insect is lost (censored) at day 4, and the rest survive to day 7. At day 2, Ŝ = 9/10 = 0.9; at day 3, two deaths among 9 at risk, Ŝ = 0.9 × 7/9 = 0.7; the censored insect leaves the risk set at day 4; at day 5, one death among 6 at risk, Ŝ = 0.7 × 5/6 = 0.583. The naive proportion surviving (5 of 10) ignores that one insect was lost before day 5.
The log-rank test compares survival in two or more groups. At each distinct event time, it compares the observed number of events in group 1 with the number expected if the hazards were equal, E₁ⱼ = dⱼn₁ⱼ/nⱼ, with hypergeometric variance Vⱼ = dⱼ(n₁ⱼ/nⱼ)(1 − n₁ⱼ/nⱼ)(nⱼ − dⱼ)/(nⱼ − 1). The statistic (O₁ − E₁)²/V, with O₁ − E₁ = Σⱼ(d₁ⱼ − E₁ⱼ) and V = ΣVⱼ, is approximately χ²₁ under the null hypothesis of equal survival; for g groups the generalisation has g − 1 degrees of freedom. A simpler approximation, Σ(O − E)²/E over groups, is slightly conservative. The log-rank test is a score test of the Cox model (Chapter 6) and is most powerful when hazards are proportional; when curves cross or differ mainly early, weighted versions (Gehan-Breslow-Wilcoxon, giving more weight to early events) can be more powerful, and stratified log-rank tests control for blocks or batches.
Survival curves should be reported with numbers at risk beneath the plot, since the right-hand tail rests on few subjects. Example interpretation: in a seed-treatment trial, treated seed lots have higher Kaplan-Meier viability curves over 12 months of storage, and the log-rank χ² of 6.2 on 1 df (p ≈ 0.013) indicates a real difference; the hazard ratio from a Cox model then states how large it is.
Cox's proportional hazards model (1972) relates the hazard to covariates: h(t | x) = h₀(t) exp(β′x), where h₀(t) is an unspecified baseline hazard and exp(βⱼ) is the hazard ratio for a one-unit increase in xⱼ, constant over time. It is semi-parametric: the covariate effects are parametric, the baseline is left free. The model has no intercept, because any constant is absorbed into h₀(t).
The coefficients are estimated by maximising the partial likelihood, the product over event times of the probability that the subject who failed was the one to fail, given the risk set: Π exp(β′xᵢ)/Σ over the risk set of exp(β′xₖ). The baseline hazard cancels, which is why it need not be specified. Tied event times are handled by Breslow's or Efron's approximation (Efron's is more accurate when ties are many), or by discrete-time models. Inference uses Wald, score and likelihood-ratio tests from the partial likelihood; the score test for a single binary covariate is the log-rank test. The baseline survival can be estimated afterwards (Breslow's estimator), giving predicted survival curves for given covariates.
A hazard ratio of exp(β) = 0.6 for a treated group means that at every time the instantaneous risk among survivors is 40% lower than in the control group; it does not mean that 40% fewer subjects die by a given time, although with modest event proportions the two are similar. Hazard ratios multiply across covariates, so a coefficient of 0.7 for a 10-unit increase in temperature means the hazard is multiplied by e^0.7 = 2.01 per 10 units.
The proportional hazards assumption must be checked: plots of log[−log Ŝ(t)] against log t for groups should be roughly parallel; scaled Schoenfeld residuals should show no trend against time (with a formal test); and adding an interaction of a covariate with time tests for a changing effect. When the assumption fails, options are stratification by the offending variable (separate baseline hazards per stratum), time-dependent covariates or coefficients, or accelerated failure time models (Chapter 7). Time-varying covariates, such as lactation number or cumulative rainfall, enter naturally through the counting-process formulation. Frailty models add random effects for clusters (animals within herds, plants within plots), the survival analogue of GLMMs. A common error is to include as a covariate something measured after the start of follow-up that depends on survival itself (immortal-time bias).
Parametric models specify the distribution of T fully. The exponential model has constant hazard λ, survival S(t) = e^(−λt), mean 1/λ and median (log 2)/λ. With right-censored data, the log-likelihood is d log λ − λΣtᵢ, where d is the number of events and Σtᵢ the total observed time (events and censoring times together), so the MLE is λ̂ = d/Σtᵢ: events per unit of time at risk, with standard error λ̂/√d. Example: 8 deaths observed in a total of 400 animal-days of follow-up give λ̂ = 0.02 per day, mean survival 50 days and median 34.7 days. Dividing 8 by the number of animals, or ignoring the censored follow-up time, gives quite different and wrong answers.
The Weibull model has S(t) = exp[−(λt)^α] and hazard h(t) = αλ(λt)^(α−1): increasing for α > 1 (wear-out, ageing), constant for α = 1 (exponential) and decreasing for α < 1. A plot of log[−log Ŝ(t)] against log t from the Kaplan-Meier estimate is a straight line with slope α if the Weibull model holds, a quick diagnostic. The Weibull is the only family that is both a proportional-hazards and an accelerated-failure-time model.
An accelerated failure time (AFT) model writes log T = μ + γ′x + σε, so covariates stretch or shrink the time scale: exp(γⱼ) is a time ratio, the factor by which a one-unit change in xⱼ multiplies survival times. With ε extreme-value, T is Weibull; with ε logistic, log-logistic; with ε normal, log-normal. Log-logistic and log-normal models give hazards that rise and then fall, as when the risk of germination failure or disease onset peaks at some intermediate time. Time ratios are often easier to communicate than hazard ratios: 'treated seed remains viable 1.4 times as long'.
Parametric models give smoother estimates, extrapolation beyond the follow-up (with due caution) and more efficient inference when the model is right; the Cox model avoids assumptions about the baseline. Model choice uses AIC, the graphical checks above and the plausibility of the implied hazard shape. Seed longevity studies use specialised probit-based viability equations (Ellis and Roberts) in which viability on the probit scale declines linearly with storage time, with slope depending on moisture content and temperature; this is a parametric survival model with normal (probit) errors fitted to germination tests over time.
Prevalence is the proportion of a population that has a disease at a point in time (point prevalence) or during a period: 30 diseased animals in a herd of 200 tested on one day give a prevalence of 0.15. Incidence measures new cases. The incidence risk (cumulative incidence, attack rate) is the proportion of initially disease-free individuals that develop disease during a specified period; the incidence rate (incidence density) is the number of new cases per unit of population-time at risk, for example 12 cases in 4,800 animal-days = 0.0025 per animal-day, or 0.91 per animal-year. Rates handle populations that change through the period and individuals followed for different times; risks need the period stated.
For a stable population with a constant incidence rate and average disease duration D, prevalence odds ≈ incidence rate × D, and for rare diseases prevalence ≈ incidence rate × D. Long-lasting conditions therefore accumulate high prevalence even with low incidence, and a cross-sectional survey favours long-duration cases (length bias, as in the inspection paradox of renewal theory). In plant pathology, incidence usually means the proportion of plants or leaves showing disease (a prevalence in the epidemiological sense), and severity the proportion of tissue affected; the terms are used differently across disciplines, so definitions should be stated.
For an exposure and a disease, the risk ratio (relative risk) RR = risk in exposed/risk in unexposed; the odds ratio OR = odds in exposed/odds in unexposed = ad/bc for a 2 × 2 table with exposed cases a, exposed non-cases b, unexposed cases c and unexposed non-cases d; and the risk difference RD = risk in exposed − risk in unexposed. Example: of 100 calves fed colostrum late, 30 develop diarrhoea; of 100 fed early, 10 do. RR = 0.3/0.1 = 3.0, OR = (30 × 90)/(70 × 10) = 3.86, RD = 0.20. The OR approximates the RR only when the disease is rare (below about 10%).
The attributable fraction among the exposed, AF_e = (RR − 1)/RR, is the proportion of disease in exposed individuals attributable to the exposure (here 2/3, if the association is causal). The population attributable fraction PAF = p_e(RR − 1)/[1 + p_e(RR − 1)], with p_e the proportion exposed, is the proportion of all disease in the population that would be prevented by removing the exposure: with half the calves fed late, PAF = 0.5 × 2/(1 + 0.5 × 2) = 0.5. Confidence intervals for RR and OR are computed on the log scale (see the categorical-data subject for SE(log OR)), and stratified estimates (Mantel-Haenszel) or regression models adjust for confounders. Association measures say nothing about causation by themselves: the design and confounding control determine that.
In a cohort study, individuals classified by exposure (vaccinated or not, fed early or late, field with or without a practice) are followed forward in time and new cases counted. Cohort studies estimate incidence risks and rates directly, give RR and RD, can study several outcomes of one exposure, and establish the time order of exposure and disease, but they are slow and costly for rare diseases. Randomised field trials are cohort studies in which exposure is assigned at random, the strongest design against confounding.
In a case-control study, individuals are selected by disease status (cases and non-diseased controls) and their past exposures compared. Because the sampling fractions of cases and controls are chosen by the investigator, risks and RR cannot be estimated directly, but the odds ratio of exposure among cases versus controls equals the odds ratio of disease among exposed versus unexposed, so case-control studies estimate the OR, which approximates the RR for rare diseases. They are efficient for rare diseases and quick, but vulnerable to selection bias (controls must represent the population that produced the cases) and recall bias. Matching cases and controls on confounders requires a matched analysis (conditional logistic regression, McNemar-type tests for pairs).
A cross-sectional study measures exposure and disease at the same time in a sample, estimating prevalence and the prevalence ratio or prevalence odds ratio. It is quick and the usual design for disease surveys of herds and fields, but it cannot establish time order and over-represents long-lasting cases.
Three families of error threaten any observational study. Selection bias arises when the subjects studied differ systematically from the target population in a way related to both exposure and disease. Information (misclassification) bias arises from imperfect measurement of exposure or disease; non-differential misclassification of a binary exposure usually biases associations towards no effect, while differential misclassification can bias them in either direction. Confounding occurs when a third factor, associated with the exposure and a cause of the disease and not on the causal pathway, distorts the association, as when farm size is associated both with use of a vaccine and with better housing. Confounding is controlled by randomisation, restriction, matching, stratified analysis (Mantel-Haenszel) or multivariable regression; it cannot be removed after the fact if the confounder was not measured.
Sample sizes follow from the methods of the hypothesis-testing manual: comparing two proportions in a cohort study, or detecting an odds ratio of a given size with a stated proportion of exposed controls in a case-control study. For surveys aimed at detecting disease (demonstrating freedom), the sample needed to find at least one positive with probability 1 − α when prevalence is at least p is approximately n = log α/log(1 − p) for a large population: about 59 animals for 95% confidence at 5% prevalence, with adjustments for imperfect test sensitivity and finite herd size.
A diagnostic test (an ELISA for a plant virus, a tuberculin test, a rapid kit for a seed-borne pathogen) is evaluated against the true disease status, established by a reference (gold-standard) test. Sensitivity Se = P(test positive | diseased) and specificity Sp = P(test negative | not diseased) are properties of the test (though they can vary with the stage of infection and the population tested). The predictive values depend also on prevalence p: PPV = Se·p/[Se·p + (1 − Sp)(1 − p)] and NPV = Sp(1 − p)/[Sp(1 − p) + (1 − Se)p]. With Se = 0.95, Sp = 0.98 and p = 0.02, PPV = 0.019/(0.019 + 0.0196) = 0.49: half the positives are false. At p = 0.30, PPV rises to 0.95. Likelihood ratios summarise a test independently of prevalence: LR+ = Se/(1 − Sp) and LR− = (1 − Se)/Sp; post-test odds = pre-test odds × LR.
The apparent prevalence from an imperfect test is AP = Se·p + (1 − Sp)(1 − p). Rearranging gives the Rogan-Gladen estimator of true prevalence, p̂ = (AP + Sp − 1)/(Se + Sp − 1). Example: Se = 0.9, Sp = 0.95 and 14% of samples positive give p̂ = (0.14 + 0.95 − 1)/(0.85) = 0.106. When Sp is imperfect and true prevalence is low, apparent prevalence can be mostly false positives.
Many tests give a continuous reading (optical density, skin-thickness increase) dichotomised at a cut-off. Raising the cut-off increases specificity and lowers sensitivity. The receiver operating characteristic (ROC) curve plots sensitivity against 1 − specificity over all cut-offs; the area under it (AUC) is the probability that a randomly chosen diseased individual has a higher reading than a randomly chosen non-diseased one (the Mann-Whitney statistic of the nonparametric manual), with 0.5 meaning no discrimination and 1 perfect discrimination. Youden's index J = Se + Sp − 1 is maximised by one common choice of cut-off; in practice the cut-off should reflect the relative costs of false positives and false negatives and the prevalence, as in Bayes decision rules.
Combining tests: in parallel interpretation (positive if either test is positive) sensitivity increases and specificity decreases; for two conditionally independent tests, Se_parallel = 1 − (1 − Se₁)(1 − Se₂) and Sp_parallel = Sp₁Sp₂. In serial interpretation (positive only if both are positive, usually by retesting positives) specificity increases: Sp_serial = 1 − (1 − Sp₁)(1 − Sp₂) and Se_serial = Se₁Se₂. Screening for a quarantine pathogen favours parallel testing (missing infection is costly); confirming before culling favours serial testing. When no perfect reference exists, latent-class models (the Hui-Walter approach) estimate Se and Sp of several tests applied in two or more populations of different prevalence, under assumptions that should be stated. Agreement between two tests or raters beyond chance is measured by Cohen's kappa.
In plant epidemiology the proportion of disease y (incidence or severity) is recorded repeatedly over time on each plot, producing a disease progress curve. Three growth models are standard. The monomolecular model, dy/dt = r_M(1 − y), suits monocyclic diseases in which inoculum does not increase during the season (many soil-borne diseases); log[1/(1 − y)] is linear in t. The logistic model, dy/dt = r_L y(1 − y), suits polycyclic diseases where new infections come from existing lesions (rusts, late blight); logit y = log[y/(1 − y)] is linear in t with slope r_L, van der Plank's apparent infection rate. The Gompertz model, with −log(−log y) linear in t, has a faster early and slower late phase than the logistic and often fits foliar epidemics well.
Example: a rust epidemic with severity 1% on day 0 and 10% on day 10 has logistic rate r = [logit 0.10 − logit 0.01]/10 = [−2.197 − (−4.595)]/10 = 0.240 per day. Under this model severity would reach 50% when logit y = 0, about (4.595/0.240) = 19.1 days after day 0. Models are fitted by linear regression on the transformed scale or, better, by non-linear least squares or binomial GLMs on the original proportions, and the fitted rates and initial levels compared between cultivars or fungicides. A fungicide that lowers the initial inoculum delays the epidemic; one that lowers r slows it; van der Plank's work showed how the two strategies combine.
The area under the disease progress curve (AUDPC) summarises a whole epidemic in one number, computed by the trapezoidal rule: AUDPC = Σ over successive assessments of [(yᵢ + yᵢ₊₁)/2](tᵢ₊₁ − tᵢ). With severity 5%, 20% and 45% on days 0, 7 and 14, AUDPC = (5 + 20)/2 × 7 + (20 + 45)/2 × 7 = 87.5 + 227.5 = 315 %-days. Because AUDPC depends on the length of the assessment period, standardised AUDPC (divided by the total duration, giving an average disease level) or relative AUDPC (as a percentage of a susceptible check or of the maximum possible) is used to compare trials of different lengths. Variants such as the area under the disease progress stairs (AUDPS) give more weight to the first and last assessments, which the trapezoidal rule under-weights.
AUDPC is analysed like any quantitative response: ANOVA in the field design, comparisons of cultivars for quantitative (partial) resistance, and correlation or regression with yield loss. It needs no growth model, which is its strength; but it loses information about the timing and shape of the epidemic, so two cultivars with very different epidemics (one early and mild, one late and severe) can have similar AUDPC. Reporting AUDPC together with the final disease level and, where useful, a fitted rate gives a fuller picture. Disease scores on ordinal scales should be converted to percentage midpoints before computing AUDPC, or analysed with ordinal models (see the nonparametric and categorical-data manuals).
A student needs to estimate LD50 and LC50 with fiducial limits from probit or logit fits, analyse parallel-line and slope-ratio assays and apply Fieller's theorem, compute Kaplan-Meier estimates and log-rank tests by hand for small examples, interpret Cox hazard ratios and check proportional hazards, fit exponential and Weibull models to censored data, compute risks, rates, RR, OR and attributable fractions, explain what each study design can estimate, evaluate diagnostic tests with predictive values and ROC curves, and compute AUDPC. Theses in entomology, pathology and animal science routinely require these.
A statistician five years into work at a plant-protection or veterinary institute analyses insecticide-resistance bioassays and reports resistance ratios with limits, validates potency assays of biopesticides and vaccines, compares survival of insects, seeds or animals under treatments with Kaplan-Meier and Cox models, designs disease surveys with sample sizes for detection and prevalence estimation, corrects apparent prevalence for test error, and analyses fungicide trials using AUDPC and progress-curve rates.
A senior statistician with twenty-five years of experience sets the analysis standards for efficacy, potency and surveillance work: the validity criteria applied to bioassays submitted for registration, the protocols for resistance monitoring, the design of national disease surveillance and freedom-from-disease surveys, and the evaluation of new diagnostic kits before adoption. Such a statistician guards against common errors such as ignoring censoring, treating ORs as RRs for common outcomes and confusing sensitivity with predictive value.
A PhD with long experience develops methods for assay, survival and epidemiological data in agriculture: hierarchical models for resistance surveillance across regions, frailty and multi-state models for animal health records, latent-class models for diagnostic tests without a gold standard, spatio-temporal models of plant-disease spread, and Bayesian approaches to freedom-from-disease surveillance. Such a researcher proves properties, validates methods by simulation and supervises doctoral students.
Derivations are sketched rather than given. Not covered in depth: competing risks and multi-state models, interval-censored survival methods, frailty models beyond a mention, quantitative (graded-response) assay designs in detail, Bayesian and latent-class diagnostic-test methods beyond a mention, spatial epidemiology, and infectious-disease transmission models. Pharmacopoeial and regulatory validity criteria for assays, and national surveillance standards, differ by country and product and are not quoted. Rules of thumb (when Fieller differs from the delta method, when OR approximates RR) are approximate. Statistical tables are not reproduced; questions state the values they need.
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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