Agricultural Statistics & Data Science · Statistical computing, data science and practice · also Statistical Consulting, Research Methodology, Technical Writing
The statistician as research partner: framing the scientist's question, choosing design and sample size, power, avoiding pseudo-replication, pre-registration, analysis plans, reporting standards, the p-value debate, ethics, and writing and presenting results. Research-methodology courses in the Agribusiness and Veterinary tracks cover the social-science and clinical sides.
In the exams: Present in AICE-JRF research-methodology units of other subjects; ASRB ARS interview (reported); professional accreditation (RSS CStat, ASA PStat) evidence of practice (heavy)
Most of the statistics done in agricultural research is done by statisticians working with scientists: agronomists, breeders, soil scientists, animal scientists, economists and extension researchers who bring questions, data and deadlines. The value a statistician adds depends less on knowing advanced methods than on turning a scientist's question into a statistical one, choosing the right experimental or sampling unit, designing studies with enough power, writing an analysis plan before the data arrive, avoiding pseudo-replication and uncontrolled multiple testing, reporting results honestly with their uncertainty, and explaining them to people who are not statisticians. Fisher's warning of 1938 still applies: to consult the statistician after an experiment is finished is often merely to ask for a post-mortem examination, to say what the experiment died of.
This manual covers the consulting interview; choosing the experimental or sampling unit; power and sample size for experiments and surveys; analysis plans and pre-registration; common errors in agricultural research, especially pseudo-replication and multiple testing; p-values, confidence intervals and the American Statistical Association's statement on p-values; reporting standards for experiments and surveys; research ethics, data integrity and authorship; writing theses, papers and technical reports; presenting statistical results to non-statisticians; and project proposals and research funding. The social-science and clinical sides of research methodology are taught in the agribusiness and veterinary tracks; here the focus is the statistician's role in agricultural research.
Doctoral examinations include research methodology in many agricultural subjects; interviews for agricultural research-service posts ask candidates how they would advise on a design or handle an ethical problem; and professional accreditation by statistical societies, such as chartered and accredited statistician schemes, requires documented evidence of consulting practice, communication and ethical conduct. Typical questions present a study description and ask for the experimental unit, the sample size, the error in the analysis, the correct interpretation of a p-value or interval, or the right response to an ethical dilemma.
Consulting begins with listening. The scientist usually arrives with a request phrased in statistical terms ('I need a t-test' or 'can you run an ANOVA?'), but the real need lies in the scientific question behind it. The first task is to understand the research objective, the subject matter and the decision the results will inform: what is being compared, under what conditions, for whom, and what difference would matter in practice. Useful questions include: What is the question you want to answer? What will you do differently depending on the answer? How were the data collected, or how will they be? What is applied to what, by whom, and how was it assigned? What is measured, when and on what? What constraints of time, land, animals, laboratory capacity and budget apply? What has been done before? Taking notes, restating the problem in the statistician's own words and asking the scientist to confirm ('so you want to know whether the new variety yields more than the local check across the three agro-ecological zones, by at least 0.3 t/ha?') prevent misunderstandings that would otherwise surface only after the analysis.
The scientific question is then translated into a statistical one: the population or conditions to which conclusions should apply; the response variables and how they are measured; the treatments or factors and their levels; the comparisons of interest, stated as estimands such as a difference in means, a ratio, a trend or a variance component; the structure of the data (blocks, sites, repeated measures, clusters); and the inference required (estimation with confidence intervals, a test of a hypothesis, prediction, or classification). Tukey's advice that 'far better an approximate answer to the right question, which is often vague, than an exact answer to the wrong question, which can always be made precise' captures the priority. Often several analyses are possible, and the choice depends on what the scientist needs to know. The statistician should also look for problems the scientist may not have noticed, such as confounding of treatments with sites, missing controls, or measurement methods that change during a study.
Consulting is a collaboration between professionals with different expertise. Clear agreement at the start on deliverables, timelines, who does what, how the statistician's contribution will be acknowledged or credited (including co-authorship where the contribution is substantial), and, in consulting units that charge, the cost, avoids later friction. Statisticians should explain the reasons for their recommendations rather than merely giving instructions, admit uncertainty, and be prepared to say no to requests that would produce misleading results, such as dropping inconvenient data or searching for any significant result. Short written summaries after each meeting record what was decided. The best outcomes come when statisticians are involved early, at the planning stage, and continue through analysis and writing, rather than being consulted only when data have already been collected.
The experimental unit is the smallest unit to which a treatment is independently applied; the observational (measurement) unit is what is measured, which may be the same or smaller. In a fertiliser trial, the plot receiving a fertiliser rate is the experimental unit, and individual plants or quadrat samples within it are observational units. In an animal feeding trial in which a ration is given to a pen of animals, the pen is the experimental unit even though each animal is weighed. In a greenhouse study in which a temperature regime is applied to a growth chamber, the chamber is the experimental unit, and if each regime is applied to only one chamber, there is no replication of the treatment at all, however many pots are in it. The number of experimental units per treatment determines the replication, the degrees of freedom for experimental error and the validity of tests; measuring more observational units within each experimental unit improves the precision of each unit's value but does not replace replication.
In surveys, the sampling unit is the unit selected by the design, and with multistage designs there are several levels: districts, villages, households, fields and crop-cutting plots. The unit of analysis should match the question: farm-level adoption is analysed per farm, but yield per hectare estimated from crop cuts within fields involves fields as units nested in farms and villages. Variances must reflect the design, because units in the same cluster resemble each other; the number of primary sampling units, not the number of final observations, often limits precision. When the question concerns a higher level (do villages with extension agents have higher adoption?), the effective sample size for that comparison is the number of villages, not the number of households.
A useful question for every study is: what was randomised, or selected, to what? Treatments randomised to plots make plots the units; varieties sown in strips across a field with only one strip each are unreplicated; treatments applied to whole villages make villages the units, even though data are collected from households. When treatments are applied at several levels, as in split-plot experiments (irrigation to main plots, varieties to subplots), each factor has its own experimental unit and error term. Mistaking the observational unit for the experimental unit is the root of pseudo-replication, discussed later, and is among the most frequent errors identified in reviews of agricultural and ecological research. Where true replication is impossible, as with a single watershed or a single long-term irrigation scheme, the limitation must be stated and conclusions framed accordingly.
Power is the probability that a study detects an effect of a specified size if it exists; conventional targets are 80% or 90%, with a significance level α of 0.05. For comparing two means with equal replication, the number of experimental units per treatment is approximately n = 2(z₁₋α/₂ + z₁₋β)²σ²/δ², where σ is the standard deviation among units and δ the smallest difference worth detecting. With σ = 0.5 t/ha, δ = 0.3 t/ha, α = 0.05 and 90% power (z = 1.96 and 1.28), n ≈ 2 × 3.24² × 0.25/0.09 ≈ 58.4, so 59 plots per treatment; with 80% power (z = 0.84), about 44. Expressed as an effect size, the standardised difference δ/σ = 0.6. The variance estimate usually comes from previous trials at similar sites, and because it is uncertain, sensitivity to its value should be checked. For more complex designs, such as randomised blocks with many treatments, factorials, split plots or multi-site trials, power is computed from the non-central F distribution or, most flexibly, by simulating data from the planned design and analysis. In agricultural trials the number of replicates is often constrained by land and cost, so power calculations are as useful for showing what a feasible design can and cannot detect as for choosing replication.
For estimating a proportion p within a margin of error e at 95% confidence by simple random sampling, n = z²p(1 − p)/e²; with p = 0.5 (the most conservative value) and e = 0.05, n = 1.96² × 0.25/0.0025 ≈ 385. For a finite population of N units, the finite population correction gives n = n₀/(1 + n₀/N): with N = 2,000, n ≈ 323. For cluster samples, the simple-random-sampling size is multiplied by the design effect, deff = 1 + (m − 1)ρ, where m is the number of units per cluster and ρ the intra-cluster correlation; with deff = 2, about 770 households are needed for the same precision. For estimating a mean, n = z²σ²/e², or in relative terms n = z²CV²/r², where CV is the coefficient of variation and r the relative margin. Sample sizes must also allow for non-response and for the precision required in subgroups such as districts, which usually dominates the total.
A sample size justification should state the outcome, the effect size or margin and why it matters, the variance assumption and its source, α, power, the design and analysis assumed, and allowances for dropout or non-response. Common pitfalls include choosing the effect size to fit the available budget and calling it 'important'; using an optimistic variance from a single trial; ignoring the cluster or block structure; and computing 'post hoc power' after a non-significant result, which adds nothing to the confidence interval and should be avoided. A non-significant result from an underpowered study is inconclusive, not evidence of no effect.
A statistical analysis plan (SAP), written before data are examined, specifies how the data will be analysed. It typically states the objectives and hypotheses; the primary and secondary outcomes and how they are derived; the design and the experimental units; the statistical model, including fixed and random effects, covariates and the handling of blocks and sites; the estimands and comparisons of interest; the significance level and the method of handling multiple comparisons; the handling of missing data, outliers and protocol deviations; the checks of model assumptions and the alternatives if they fail (transformations, generalised models); planned subgroup and sensitivity analyses; and the tables and figures to be produced. Writing the plan forces clarity about the question and often reveals design problems while they can still be fixed. In regulated settings, such as registration trials of pesticides or veterinary medicines, analysis plans are formal requirements; in research, they are increasingly expected by funders and journals.
Pre-registration places the study plan and analysis plan in a time-stamped public or embargoed registry before data collection or analysis. It distinguishes confirmatory analyses, specified in advance, from exploratory ones, suggested by the data, and so protects against the 'garden of forking paths', the many analytic choices (which outcome, which covariates, which subset, which transformation) that can, consciously or not, be steered towards significant results. Registered reports go further: journals review the introduction and methods before the results are known and accept the paper in principle if the study is conducted as planned, removing the incentive to publish only positive results. Clinical trials have long required registration; in agricultural and environmental sciences pre-registration is less common but growing. Pre-registration does not forbid deviations or exploration: deviations are reported and justified, and exploratory findings are presented as such, as hypotheses for further testing rather than as confirmed results.
Pseudo-replication, named by Hurlbert in 1984, is the use of inferential statistics to test for treatment effects with data in which treatments are not replicated or replicates are not statistically independent. It takes several forms in agricultural research. Simple pseudo-replication treats subsamples as replicates, as when each of two irrigation treatments is applied to one large field and many plants per field are analysed as if they were replicates. Temporal pseudo-replication treats repeated measurements on the same unit over time as independent. Sacrificial pseudo-replication has genuine replicates but pools their subsamples, discarding the replicate structure. Pseudo-replication also arises in multi-location trials when site-by-treatment interaction is ignored and plots across sites are pooled as if from one experiment, and in surveys when households in the same village are treated as independent for village-level comparisons. Its effect is to understate the variance of treatment comparisons and inflate the apparent significance. Remedies are to replicate the treatment on independent experimental units; to analyse at the level of the experimental unit, for example using plot means; and to use mixed models with random effects for units, sites and repeated measures.
When many hypotheses are tested, the chance of false positives rises. With 20 independent tests of true null hypotheses at α = 0.05, one false positive is expected, and the probability of at least one is 1 − 0.95²⁰ ≈ 0.64. Agricultural research invites multiplicity: many traits measured on the same trial, many pairwise comparisons among varieties, many sites, many time points and many subgroups. The family-wise error rate, the probability of any false positive, is controlled by the Bonferroni correction (testing each of m hypotheses at α/m, 0.05/20 = 0.0025), Holm's step-down method (uniformly more powerful), and, for all pairwise comparisons among means, Tukey's HSD; Dunnett's method compares several treatments with a control. When many tests are exploratory, as in genomics, the false discovery rate, the expected proportion of false positives among rejections, is controlled by the Benjamini–Hochberg procedure, which ranks p-values and rejects those with p₍ᵢ₎ ≤ (i/m)q. The least significant difference test without protection inflates the error rate across many comparisons. The best defences are to define a small number of primary questions in advance, to use planned contrasts that answer them, and to report all tests performed rather than only the significant ones.
Reviews of published agricultural research repeatedly identify further problems: treating a numeric code for blocks or sites as a continuous covariate; using multiple-range tests such as Duncan's on quantitative treatment levels instead of fitting response curves; ignoring the design (analysing a split plot as a randomised block); failing to check assumptions, or transforming data without back-transforming estimates sensibly; confusing statistical significance with practical importance; interpreting non-significant results as proof of no effect; comparing significance levels instead of testing differences ('A was significant and B was not, so A differs from B'); dichotomising continuous variables; and extrapolating beyond the range of data or the population sampled. Each is avoidable with early statistical involvement and careful review.
Agricultural research increasingly tests technologies on farmers' fields rather than research stations, which brings realism but also statistical challenges. Farms differ in soil, management and weather, so treatment effects vary between farms and the farm, not the plot, is often the key unit; designs place each treatment, or a small set, on every farm so that farms act as blocks, and analyses estimate both the mean effect and its variation across farms, which tells farmers how likely a technology is to pay on their land. Farmer-managed trials have more missing data and protocol deviations than researcher-managed ones, which must be recorded rather than ignored. Large crowd-sourced or 'tricot' style trials, in which many farmers each test a few varieties and rank them, use incomplete block and ranking models to combine the results. The statistician's role is to keep the design simple enough for farmers to manage while preserving randomisation and enough replication across farms.
A p-value is the probability, computed assuming the null hypothesis and all other model assumptions are true, of obtaining a test statistic at least as extreme as the one observed. It measures how incompatible the data are with a specified statistical model. It is not the probability that the null hypothesis is true, not the probability that the result occurred by chance, and not a measure of the size or importance of an effect: a tiny, unimportant difference can give a very small p-value in a large study, and a large, important difference can give a large p-value in a small one. The American Statistical Association's 2016 statement on statistical significance and p-values set out six principles: p-values can indicate how incompatible the data are with a specified model; they do not measure the probability that the studied hypothesis is true or that the data were produced by chance alone; scientific conclusions and business or policy decisions should not be based only on whether a p-value passes a specific threshold; proper inference requires full reporting and transparency; a p-value does not measure the size of an effect or the importance of a result; and by itself a p-value does not provide a good measure of evidence regarding a model or hypothesis. A 2019 editorial in the association's journal went further and recommended abandoning the phrase 'statistically significant', a proposal that remains debated.
Confidence intervals show both the size of an effect and its precision. A 95% confidence interval is produced by a procedure that, over repeated samples, contains the true parameter 95% of the time; for a mean yield difference of 0.42 t/ha with standard error 0.15, an approximate 95% interval is 0.42 ± 1.96 × 0.15, from about 0.13 to 0.71 t/ha. The interval shows that the data are compatible with differences from small to substantial, which a bare p-value hides. An interval excluding zero corresponds to a two-sided test significant at the 5% level, but the interval also shows whether the effect could be smaller than a practically important threshold. For decision-oriented agricultural research, comparing the interval with a minimum important difference, such as the yield gain needed to pay for a new input, is more informative than a significance test. Equivalence and non-inferiority tests, which ask whether a difference is within a pre-specified margin, address questions such as whether a cheaper fertiliser source performs as well as the standard.
Statisticians should report effect estimates with confidence intervals, give exact p-values rather than thresholds, avoid language such as 'trend towards significance' or 'highly significant' as substitutes for effect sizes, interpret results in the light of prior evidence, study quality and plausibility, and present non-significant results as uncertain rather than as evidence of no effect. Bayesian methods offer an alternative, giving posterior probabilities for effects and credible intervals, and are increasingly used where prior information exists, such as in variety evaluation across many trials.
Reviews of published research in many fields have found that essential information, such as how units were randomised, how sample sizes were chosen, how many units were lost and why, and exactly which analysis was done, is often missing, making studies impossible to evaluate, replicate or include in meta-analyses. Reporting guidelines list the items a report should contain. The CONSORT statement for randomised controlled trials, first published in 1996 and updated since, includes a checklist and a flow diagram of participants through enrolment, allocation, follow-up and analysis. The ARRIVE guidelines cover research using animals, the REFLECT statement adapts CONSORT to livestock trials and food-safety studies, STROBE covers observational studies, and PRISMA covers systematic reviews. Agricultural field experiments have no single universal guideline, but the same principles apply, and journals in agronomy and crop science increasingly publish checklists of essential items.
For designed experiments, a complete report describes the objectives and hypotheses; the site, soil, climate and season; the experimental design, including the experimental unit, plot size and borders, number of replicates and how sample size was decided; the randomisation method; the treatments in enough detail to repeat them; measurements and their timing, including any subsampling; any losses of units and their reasons; the statistical model, including fixed and random effects, software and version; and results as estimated means or differences with standard errors or confidence intervals, not only letters indicating significance. For multi-site trials, the results by site and the treatment-by-site interaction should be shown. For surveys, reports describe the target population and sampling frame, the sample design (stratification, clustering, selection probabilities), the sample size and response rates, the weighting and calibration methods, the questionnaire or measurement protocols, data-quality procedures, the estimation and variance-estimation methods, and the margins of error of key estimates. National statistical offices follow quality frameworks, such as those based on the United Nations Fundamental Principles of Official Statistics, that require documentation of relevance, accuracy, timeliness, accessibility, coherence and comparability.
Statisticians have ethical obligations to the integrity of their work, to the people and organisations they work for, to research subjects and to society. Professional codes, such as the International Statistical Institute's Declaration on Professional Ethics and the American Statistical Association's Ethical Guidelines for Statistical Practice, and the codes of national statistical societies that award accredited or chartered status, set out common principles: use methods appropriate to the question and data and be honest about their limitations; do not let funders, clients or employers determine conclusions; disclose conflicts of interest; protect the confidentiality of respondents and data; report all relevant results, not just favourable ones; and correct errors when they are found. Statisticians often face pressure to produce a desired result: to drop 'outliers' that weaken a treatment effect, to switch to whichever outcome gives significance, or to describe an exploratory finding as confirmatory. The professional response is to explain why such practices mislead, offer legitimate alternatives such as sensitivity analyses, document decisions, and, if necessary, decline to put one's name to the work.
Research misconduct comprises fabrication (inventing data), falsification (manipulating data, materials or processes, or omitting data, so that the record is misrepresented) and plagiarism. Statisticians are often the people best placed to detect problems, because data that are too good, digit patterns that are implausible, duplicated rows, values inconsistent with field records or impossible variances can indicate error or misconduct. Questionable research practices, including p-hacking, HARKing (hypothesising after results are known), selective reporting and inappropriate exclusion, are more common than outright misconduct and also distort the literature. Data integrity is protected by keeping raw data unchanged, documenting every processing step in code, maintaining audit trails, archiving data and code, and making them available for verification. When a statistician suspects misconduct, institutional procedures for confidential reporting should be followed, and whistle-blowers acting in good faith should be protected.
Authorship carries credit and responsibility. Widely used criteria, such as those of the International Committee of Medical Journal Editors, require substantial contributions to conception or design, or to acquisition, analysis or interpretation of data; drafting or critically revising the work; approval of the final version; and agreement to be accountable for the work. A statistician who designs a study, plans and conducts the analysis, interprets results and helps write the paper meets these criteria and should be an author; a statistician who only runs a routine analysis on request may be acknowledged instead. Contributor role taxonomies, such as CRediT, describe each person's contribution, for example 'formal analysis' or 'methodology'. Gift authorship for senior staff who did not contribute and ghost authorship that hides real contributors are unethical. Authorship should be discussed and agreed at the start of a collaboration and revisited as roles change.
Most research writing follows the IMRaD structure: introduction (the problem, what is known, the gap, the objectives), methods, results and discussion. Theses add a literature review and often several research chapters, each structured like a paper, with general introduction and conclusions. The statistical part of the methods section should allow a competent reader to repeat the analysis: the design and experimental units, the number of replicates and why, the randomisation, the variables and how they were derived, the statistical model with fixed and random effects written explicitly or in words, how assumptions were checked and what was done if they failed, how multiple comparisons were handled, the treatment of missing data and outliers, and the software and versions used. Phrases such as 'data were analysed by ANOVA using standard software' are inadequate. Methods should be described in the past tense, and any departures from the original plan explained.
Results should present the findings in a logical order, answering the stated objectives, with estimates, measures of uncertainty and test results, but without interpretation, which belongs in the discussion. Tables give exact values and suit detailed comparisons; figures show patterns, trends and interactions. Good tables have informative titles, units, consistent and sensible decimal places (yields in t/ha to one or two decimals, not six), standard errors or confidence intervals, and the number of observations; letters indicating significance groups, if used, should not replace estimates of differences. Good figures show the data where possible, label axes with variables and units, use error bars that are defined in the caption (standard error, standard deviation or confidence interval), avoid three-dimensional effects and dual axes that distort, and remain readable in grey-scale and by readers with colour-vision deficiency. For factorial and multi-site experiments, interaction plots communicate better than long tables of means.
Technical reports for managers, ministries and funding agencies put the main findings and recommendations first, in an executive summary written in plain language, with methods and detailed results in later sections and appendices. The discussion of a paper or thesis interprets the results: what they mean for the question, how they compare with previous studies, the strengths and limitations of the study (including power, generality across sites and seasons, and possible biases), and the implications for practice and further research. Claims should be proportional to the evidence: a single-season, single-site trial does not establish a general recommendation. Statisticians reviewing drafts should check that conclusions follow from the analysis, that uncertainty is acknowledged, and that numbers in the text match those in tables.
Peer review often raises statistical points, and statisticians help authors respond. A good response addresses every comment, explains what was changed and where, and gives reasoned arguments, with references, where the authors disagree. When a reviewer asks for an analysis that would be inappropriate, such as multiple-range tests on quantitative factor levels, the response should explain why another analysis answers the question better and, if helpful, show both. When a reviewer identifies a genuine error, it should be corrected openly, even if conclusions change. Courteous, complete responses shorten the review process and build the authors' credibility with editors.
Farmers, extension officers, managers, policymakers and journalists need statistical results to make decisions, but most are not statisticians. Effective communication starts with the audience's question and the decision they face, and leads with the answer: 'the new variety yielded on average 0.4 t/ha more than the local variety across 24 farms; on about four farms in five it did better'. Technical terms are replaced or explained: instead of 'significant at p < 0.05', say how large the difference is and how sure we are; instead of 'heterogeneity of variance', say that results varied more in some places than others. Numbers are rounded to the precision that matters, and units are those the audience uses, such as bags per acre or kilograms per hectare, with conversions where necessary. Absolute changes are often clearer than relative ones: 'disease incidence fell from 20% to 10%' is clearer than 'a 50% reduction', and both together are clearest.
Uncertainty must be conveyed, not hidden, but in forms people understand. Ranges ('between 0.1 and 0.7 t/ha'), natural frequencies ('in 8 of every 10 seasons') and visual displays (intervals on charts, many plausible outcomes shown as fan charts or dot plots) work better than standard errors. For forecasts, such as seasonal rainfall outlooks or crop production estimates, probabilistic statements ('a 60% chance of above-normal rainfall') should be explained with what they mean for decisions, and verification of past forecasts builds trust. It is important to distinguish what is known from what is assumed, to say where results apply (these soils, these seasons) and where they may not, and to avoid overconfidence that will be exposed if outcomes differ.
Graphs are often more persuasive than tables for non-specialists: a simple bar or dot chart with intervals comparing varieties, a map of yield gaps, or a line chart of prices over time. Each slide or figure should carry one message, stated in its title ('Variety B outyields the check in wet seasons only'). Presentations to farmers may use demonstrations, field days, local examples and pictures more than charts. Interactive dashboards let managers explore results but need careful design and explanation. Throughout, the statistician should check understanding by inviting questions and asking listeners to restate the key finding, and should be honest when the data cannot answer the question asked.
A research proposal must convince reviewers that the question matters, that the design will answer it and that the team can deliver. Typical sections are a summary; background and justification; objectives and hypotheses; methods, including design, sample size and its justification, data collection, quality control and analysis plan; a work plan with milestones; expected outputs, outcomes and impact pathways; risks and their mitigation; a data management plan; ethics and permits; the team and partners; and a budget with justification. Development funders frequently require a logical framework (logframe) linking activities to outputs, outcomes and goals, with indicators, means of verification and assumptions, or a theory of change describing how and why the project is expected to lead to impact. Objectives should be specific, measurable, achievable, relevant and time-bound. A clear statistical design section, with a power calculation and an analysis plan, strengthens a proposal because reviewers increasingly look for them.
Statisticians should be involved when proposals are written, not after funding is awarded, because design decisions made at that stage, such as the number of sites, seasons, farms or animals, are fixed by the budget. A statistician can check that objectives are answerable, that the design has adequate power, that the sampling plan reaches the intended population, that monitoring and evaluation indicators are measurable, and that time and money are budgeted for data management and analysis, which are often underestimated. Including statistical time in the budget, as a named team member or a consulting allocation, is good practice and is required by some funders. Evaluation designs for development projects, such as randomised or quasi-experimental impact evaluations with baseline and endline surveys and comparison groups, need statistical input from the start, since impact cannot be measured credibly afterwards without a baseline or counterfactual.
Once funded, projects should register studies where appropriate, finalise analysis plans before data collection, set up data management systems, and report progress against milestones honestly, including problems. Interim analyses should be planned rather than repeated informally, since looking repeatedly at accumulating data inflates false-positive rates unless adjusted. At the end, results should be published regardless of direction, data archived according to the data management plan, and lessons recorded for future proposals. Reviewing others' proposals for funding agencies is also part of a statistician's professional service and a good way to learn what works.
A postgraduate student uses this subject in thesis work and in assisting a consulting unit: interviewing a scientist to clarify a question, identifying the experimental unit in a described trial, calculating sample sizes for an experiment and a survey, writing an analysis plan, spotting pseudo-replication and uncontrolled multiple testing in a draft paper, interpreting p-values and confidence intervals correctly, and writing a clear methods section. In examinations and interviews, students are asked to diagnose errors in study descriptions and to explain results in plain language.
A statistician five years into practice consults with many scientists each season: helping plan trials and surveys, setting replication with power calculations, writing analysis plans, analysing data with appropriate mixed models and multiplicity control, reviewing manuscripts, and presenting results to managers and farmers. They decide when to push back on requests that would mislead, how to explain why plots, not plants, are the replicates, and how to communicate uncertainty in forecasts and recommendations. Their name on a paper signals that the statistics are sound.
A senior statistician with twenty-five years of experience leads a consulting unit or a statistics department in a research institute or agency: setting standards for design review, analysis plans and reporting, training scientists in research methods, sitting on proposal and ethics committees, resolving authorship and integrity disputes, and advising leadership on the evidence behind policy and investment decisions. They decide which projects need intensive statistical involvement and make the case for budgeting statistical time in proposals. They also build the unit's reputation by making sure that its advice is consistent, documented and defensible.
A researcher with a PhD and long experience studies research practice itself: the prevalence and consequences of pseudo-replication and multiplicity in agricultural literature, methods for design and analysis of complex multi-environment and on-farm trials, approaches to communicating uncertainty to decision makers, and the reproducibility of agricultural research. Such researchers develop guidelines and checklists, teach consulting and research methods, mentor young statisticians, assess candidates for professional accreditation and serve as statistical reviewers for journals and funders. They also study how statisticians and scientists collaborate best.
This manual covers consulting and research methods from the statistician's side; it does not cover qualitative research methods, social-science survey questionnaire design in depth, or clinical trial regulation, which are taught in other tracks. Reporting guidelines and ethical codes are summarised, not reproduced, and are revised periodically, so current versions should be consulted. Sample-size formulas given are normal approximations for simple designs; complex designs need simulation or specialist methods.
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.
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