Sustainability & Environment (Agri-Food Systems) · Postgraduate & Professional Advanced · also Research Methodology, Experimental Design for Environmental Science, Scientific Writing and Research Ethics
Designing, analysing and publishing environmental research: hypotheses, field and laboratory designs, long-term experiments, mixed methods, meta-analysis, reproducibility and ethics.
In the exams: UGC NET Paper 1 (research aptitude) and Unit 9; ICAR AICE-JRF/SRF; PhD coursework
Research methods are the rules that turn curiosity about the environment into evidence other people can trust. Environmental and sustainability science adds its own difficulties to the general logic of research: the units of interest (a catchment, a forest, a farm, a community) are large, few, variable and impossible to randomise; effects unfold over decades; observations close together in space and time are not independent; and many questions involve people as much as ecosystems. This manual covers the full cycle of an environmental study, from framing a question to publishing the result.
It begins with research questions and hypotheses and the general logic of scientific inference, then treats experimental design at field, plot and landscape scale, long-term experiments and monitoring, and before-after-control-impact designs for assessing human impacts. It moves to the statistical tools that environmental data demand beyond a first course: mixed-effects models and repeated measures, multivariate methods for community data, and spatial statistics and geostatistics. It then covers qualitative and participatory methods and mixed-methods designs, systematic review and meta-analysis, open data, reproducibility and research ethics, and finally scientific writing, publication and peer review.
Basic statistics (descriptive measures, distributions, t, F and chi-square tests, simple regression, classical designs such as completely randomised and randomised block) are taught in the Quantitative Methods subject of this track and in depth in the Agricultural Statistics track; here they are used, not re-derived.
The subject is examined in two ways. General research-aptitude papers, set for lecturer eligibility and doctoral admission in many countries, ask about types of research, the steps of the research process, hypotheses, sampling, ethics, referencing and the structure of theses and articles. Subject papers for environmental-science fellowships, agricultural research services and PhD coursework ask about design choices (pseudoreplication, blocking, BACI), model choices (fixed versus random effects, ordination methods, kriging) and short calculations: power and sample size, Bray–Curtis dissimilarity, nearest-neighbour ratios, response ratios and heterogeneity statistics, impact factors and h-indices. Professional ecologist certifications expect the same design judgement applied to real projects.
Research is systematic inquiry that produces new, verifiable knowledge. It is classified in several overlapping ways. By purpose, fundamental (basic) research seeks general understanding, applied research addresses a practical problem, action research is carried out by practitioners to improve their own practice in cycles of planning, acting, observing and reflecting, and evaluation research judges whether a programme or policy achieved its aims. By approach, quantitative research measures and tests with numbers, qualitative research interprets meanings, experiences and processes, and mixed-methods research combines both deliberately. By design, experimental research manipulates a factor and controls others, quasi-experimental research compares groups that were not randomly assigned, descriptive (observational) research records conditions as they are, correlational research examines associations, and historical research reconstructs past states from records, archives or proxies such as pollen and tree rings. Reasoning may be deductive, from a general theory to a specific prediction to be tested, or inductive, from specific observations to a general pattern; abductive reasoning proposes the most plausible explanation for a surprising observation. The research process usually follows these steps: identify a problem and review the literature; formulate a question and hypotheses; choose a design and define variables; select a sample and methods of data collection; collect and analyse data; interpret results against hypotheses; and report and archive. The steps are iterative: a literature review often reshapes the question, and a pilot study often reshapes the methods. A research proposal sets out the background and gap, objectives, hypotheses, methods, expected outputs, timeline, budget, risks and ethical approvals.
A good research question is specific, answerable with available methods and data, and important to someone. For environmental reviews and interventions, frameworks such as PICO or PECO structure it: Population (what system or organisms), Intervention or Exposure, Comparator, and Outcome. A hypothesis is a testable, falsifiable statement about the answer. Karl Popper argued that science advances by trying to falsify hypotheses rather than prove them; a hypothesis that no possible observation could contradict is not scientific. In statistical testing, the null hypothesis (H₀) states no effect or no difference, and the alternative (H₁) states the effect of interest; a directional alternative supports a one-tailed test. Chamberlin's method of multiple working hypotheses and Platt's strong inference recommend stating several rival explanations and designing studies that discriminate between them, which guards against attachment to a favourite idea. Variables are defined operationally, that is, by how they will be measured. The independent (explanatory) variable is manipulated or observed as a cause; the dependent (response) variable is the outcome; a confounding variable is associated with both and can create a spurious relation; a mediating variable lies on the causal path between them; a moderating variable changes the strength or direction of the relation. Two errors are possible in testing. A Type I error rejects a true null hypothesis; its probability is the significance level α, often set at 0.05. A Type II error fails to reject a false null hypothesis; its probability is β, and the power of a test is 1 − β, conventionally targeted at 0.8 or more. A p-value is the probability of data at least as extreme as those observed if the null hypothesis were true; it is not the probability that the null hypothesis is true, and a non-significant result is not evidence of no effect when power is low.
R.A. Fisher's three principles of experimental design are replication, randomisation and local control (blocking). The experimental unit is the smallest unit to which a treatment is independently applied: a plot, a pot, a pond, a cage, a catchment. Replication means applying each treatment to several experimental units, which allows experimental error to be estimated. Randomisation assigns treatments to units by chance, protecting against systematic bias from unknown gradients. Blocking groups similar units together, for example plots at the same slope position, and applies every treatment within each block, removing block-to-block variation from the error term. Stuart Hurlbert (1984) named the commonest error in field ecology pseudoreplication: using inferential statistics to test for treatment effects with data from experiments where treatments are not replicated or replicates are not statistically independent. Simple pseudoreplication treats several samples from one treated unit (ten soil cores from one fertilised plot) as replicates; temporal pseudoreplication treats repeated measurements of the same unit over time as independent; sacrificial pseudoreplication pools data from true replicates before analysis, discarding the information on between-unit variance. Subsamples are valuable for estimating the unit mean precisely but do not add degrees of freedom for testing treatments. In classical designs the error degrees of freedom are: completely randomised design (CRD) with t treatments and r replicates, t(r − 1); randomised complete block design (RCBD), (t − 1)(r − 1); Latin square with t treatments, (t − 1)(t − 2). The split-plot design applies one factor to large whole plots and another to subplots within them, giving two error terms: whole-plot effects are tested against the whole-plot error, which has fewer degrees of freedom, so they are estimated less precisely. Factorial designs test several factors and their interactions together.
Plot size and shape trade precision against cost and edge effects. Larger plots average out small-scale heterogeneity, and guard rows or buffer zones prevent treatment effects (fertiliser drift, root foraging, shading) from crossing between plots; measurements are taken from the inner net plot. Uniformity trials and the Smith variance law relate plot size to variance. The number of replicates needed is found by power analysis before the study. For comparing two means with a two-sided test, an approximate number per group is n = 2(zα/2 + zβ)² σ² / δ², where σ is the standard deviation and δ the smallest difference worth detecting; with α = 0.05 (z = 1.96) and power 0.8 (z = 0.84), n ≈ 15.7 (σ/δ)², so detecting a difference equal to one standard deviation needs about 16 units per group, and halving δ quadruples n. At landscape scale, where treatments such as fire regimes, land-use change or dams cannot be replicated or randomised, researchers rely on other designs. Natural experiments exploit events or policies that created comparable treated and untreated areas. Gradient designs sample along a continuous driver such as elevation, rainfall, nitrogen deposition or urban intensity and fit regression rather than ANOVA, which often gives more information per sample. Space-for-time substitution uses a chronosequence of sites of different ages (for example abandoned fields of different years since abandonment) to infer change over time; it assumes sites differ only in age and share the same history, an assumption that frequently fails. Large manipulative experiments do exist: whole-catchment clearing, whole-lake fertilisation, free-air carbon dioxide enrichment rings and large forest fragmentation experiments. Observational studies must deal with confounding by design (matching, stratification) and analysis (covariates), and should state causal assumptions explicitly, for example with directed acyclic graphs.
Many environmental processes are slow, episodic or delayed: soil organic carbon changes over decades, forests turn over over centuries, and droughts, floods, fires and pest outbreaks are rare events whose effects persist. Short studies, typically three years in a funded project, miss these and can produce misleading conclusions, such as a fertiliser effect that reverses as soil acidifies, or a species decline that is one phase of a natural cycle. The oldest continuing agricultural field experiments began in the nineteenth century: the Broadbalk wheat experiment at Rothamsted in England (1843) and the Park Grass experiment (1856), the Morrow Plots in Illinois (1876) and the Askov experiments in Denmark (1894); long-term fertiliser and rotation experiments established later in Asia, Africa and Latin America have shown how yields and soil properties respond to decades of contrasting management. Their archived soil and crop samples have answered questions their founders could not imagine, such as the history of atmospheric pollutants and radioactive fallout. Ecological networks extend this approach: national long-term ecological research networks, starting in the United States in 1980, and the international network linking them; regional infrastructures in Europe and Australia; and global networks of large forest dynamics plots in which every stem above 1 cm diameter is mapped and remeasured every few years, beginning with a 50 ha plot on Barro Colorado Island in Panama. Flux tower networks measure carbon, water and energy exchange continuously. The value of long-term work lies in detecting trends, quantifying variability, capturing extreme events and lag effects, testing models over long periods and providing platforms for new questions.
Monitoring is repeated measurement to detect change. Lindenmayer and Likens distinguish passive (curiosity-driven, no question), mandated (required by law, often without design) and question-driven monitoring, and argue for adaptive monitoring, in which questions, conceptual models and designs evolve while key measurements remain consistent. A good monitoring programme begins with clear objectives and a conceptual model of the system, chooses indicators that respond to the drivers of interest, and uses a statistical design capable of detecting a specified change, such as a 20 percent decline over ten years, with stated power. Permanent plots, remeasured over time, are more powerful than new random plots for detecting change because each plot serves as its own control; rotating panels combine both. Sampling frequency should match the dynamics of the variable and avoid aliasing with seasonal or diurnal cycles. Detecting a trend depends on its size, the length of the record and year-to-year variability; serial correlation reduces effective sample size. Long-term experiments face their own problems: treatments are modified over the years (new varieties, changed rates), methods and instruments change, and staff turn over. Good practice includes overlap periods when methods change, calibration between old and new instruments, rigorous metadata, archiving of samples, and stable funding with institutional commitment. Analysis must respect the history: a treatment change in year 60 creates a new experiment that is not replicated in time. The shifting baseline syndrome, in which each generation takes the degraded state it first knew as normal, is one reason why long records and historical data matter for setting restoration targets. Citizen-science programmes, such as bird counts and phenology networks, provide long records over large areas if protocols and observer effort are recorded and analysed.
Environmental impact studies ask whether a development, pollution event or management intervention changed something. Two simple designs are weak. A before–after (BA) comparison at the impact site confounds the impact with any other change over time, such as a wet year. A control–impact (CI) comparison after the event confounds the impact with pre-existing differences between sites. Green (1979) proposed combining both: sample the impact site and a control site, both before and after the event. In a before-after-control-impact (BACI) design, the impact is the interaction between period (before, after) and location (control, impact): the change at the impact site minus the change at the control site. For example, if mean invertebrate density at a control stream goes from 120 to 110 per sample and at the impact stream from 125 to 80, the BACI estimate is (80 − 125) − (110 − 120) = −45 − (−10) = −35 per sample. The same logic in economics is called difference-in-differences, and it rests on a key assumption: without the impact, the two sites would have followed parallel trends. A single sample before and after at one control and one impact site gives no measure of natural variability. Stewart-Oaten and colleagues (1986) proposed BACI with paired series (BACIPS): sample control and impact simultaneously on many dates before and after, and test whether the mean difference between them changed; replication in time estimates natural variability of the difference, although serial correlation must be checked. Underwood (1991, 1994) argued that one control is not enough, because two sites may drift apart for reasons unrelated to the impact, and proposed asymmetrical designs with multiple control sites and one impact site, analysed with ANOVA that compares the impact site's change with the variability among controls.
BACI designs are central to environmental impact assessment follow-up, restoration evaluation and evaluation of conservation interventions, but they require planning before the impact occurs, which is often the hardest part. Practical points include: choosing several controls that resemble the impact site in habitat and history but are far enough away to be unaffected; sampling at multiple times before and after to capture variability at the right temporal scale; measuring several response variables linked by a conceptual model to the expected impact; and fixing the analysis plan and effect size of concern in advance. When the impact is a gradient rather than a point, such as distance from a discharge, before-after-gradient designs regress the response on distance before and after. When no before data exist, researchers use CI designs with many controls and covariates, or reconstruct the before state from archives, remote sensing or sediment cores, while stating the weaker inference. The beyond-BACI approach also distinguishes pulse responses (a temporary change that recovers) from press responses (a sustained change), and the design must sample long enough after the impact to tell them apart. Analysis today usually uses mixed-effects models with site and sampling time as random effects, and the BACI interaction as the fixed effect of interest; generalised linear mixed models handle counts and proportions. Randomised versions, in which treatments are assigned at random to several units with before and after data, give the strongest causal inference and are increasingly used for evaluating agri-environment and conservation programmes. Studies comparing designs have shown that weaker designs (CI or BA alone) can give biased and even reversed estimates compared with BACI and randomised designs, which is a strong argument for investing in baseline data.
Environmental data are usually grouped: plots within sites, trees within plots, repeated visits to the same plot, animals within herds. Observations within a group are more similar to each other than to observations in other groups, so treating them as independent overstates the information in the data and inflates Type I error. Mixed-effects models handle this by including random effects alongside fixed effects. A fixed effect is a factor whose levels are of direct interest and would be the same in a repeat of the study, such as fertiliser treatment or forest type; its coefficients are estimated directly. A random effect is a grouping factor whose levels are a sample from a larger population, such as sites, years or observers; the model estimates the variance among levels rather than each level's effect, and inference extends to the population of levels. A random intercept allows each group its own baseline; a random slope allows the effect of a covariate to vary among groups. Random effects can be nested (plots within sites, each plot belongs to one site) or crossed (every species measured at every site). The intraclass correlation coefficient, ICC = σ²between / (σ²between + σ²within), measures how strongly observations cluster; an ICC of 0.6 means 60 percent of the variance lies between groups. A common rule of thumb is that a grouping factor needs at least five or so levels for its variance to be estimated usefully; with fewer, treat it as fixed. Variance components are estimated by restricted maximum likelihood (REML), which reduces the downward bias of maximum likelihood (ML) estimates of variance; models that differ in fixed effects are compared using ML fits. Mixed models also solve pseudoreplication: subsamples enter as observations within a random effect for the experimental unit, so treatments are tested against between-unit variation.
Repeated measures on the same units over time, such as monthly soil respiration from the same chambers, create correlation that decreases with time lag. Classical repeated-measures ANOVA assumes sphericity, equal variances of differences between all pairs of times, tested with Mauchly's test and corrected with the Greenhouse–Geisser or Huynh–Feldt adjustments to degrees of freedom. Mixed models offer more flexibility: compound symmetry assumes the same correlation between any two times; a first-order autoregressive structure, AR(1), assumes correlation ρ at lag one, ρ² at lag two and so on; unstructured covariance estimates every pair separately at the cost of many parameters. Mixed models also cope with unbalanced data and missing observations, common in field work. Many environmental responses are not normal. Generalised linear models (GLMs) use a link function and an error distribution suited to the data: counts with a Poisson distribution and log link, proportions or presence–absence with a binomial distribution and logit link. Overdispersion, when variance exceeds the mean in count data, is common and is handled with negative binomial or quasi-Poisson models or an observation-level random effect; excess zeros may need zero-inflated or hurdle models. Generalised linear mixed models (GLMMs) combine non-normal errors with random effects. Model selection uses information criteria: Akaike's information criterion, AIC = 2k − 2 ln L, where k is the number of parameters and L the maximised likelihood, rewards fit and penalises complexity; models within about 2 AIC units of the best have substantial support, and model averaging combines them. Residual plots, checks of random-effect distributions and the number of groups must be reported. Degrees of freedom for tests in mixed models are approximate, and methods such as Kenward–Roger or Satterthwaite are used.
Community data, the abundance of many species at many sites, are multivariate, sparse (full of zeros) and non-normal. Multivariate methods summarise such data and relate them to environmental variables. The first choice is a measure of resemblance between sites. Euclidean distance suits environmental variables after standardisation but is poorly suited to species data because of the double-zero problem: two sites both lacking a species would appear similar for that reason. The Bray–Curtis dissimilarity, BC = 1 − 2C / (S₁ + S₂), where C is the sum of the lesser counts of each species shared by the two sites and S₁ and S₂ are the total counts at each site, ignores double zeros and ranges from 0 (identical) to 1 (no species in common). For presence–absence data the Jaccard similarity is a / (a + b + c), where a is the number of shared species and b and c the species unique to each site; the Sørensen index is 2a / (2a + b + c). Ordination arranges sites (and species) along a few axes so that similar sites are close. Principal component analysis (PCA) uses Euclidean distance and assumes linear responses; it suits environmental data and short gradients. Correspondence analysis (CA) and detrended correspondence analysis (DCA) assume unimodal species responses, appropriate for long gradients; a widely used rule of thumb reads DCA gradient length above about 4 standard deviation units as favouring unimodal methods and below about 3 as favouring linear methods. Principal coordinates analysis (PCoA) works with any distance measure. Non-metric multidimensional scaling (NMDS) preserves the rank order of dissimilarities and makes no assumption about response shape; its stress value measures fit, and Clarke's guidelines treat stress below 0.05 as excellent, below 0.1 as good, below 0.2 as usable and above 0.2 as poor. Constrained (direct) ordination, redundancy analysis (RDA, linear) and canonical correspondence analysis (CCA, unimodal), extracts only the variation explained by measured environmental variables and tests it by permutation.
Cluster analysis groups sites into types. Hierarchical agglomerative methods join the most similar sites and groups step by step, with linkage rules that define group similarity: single linkage (nearest neighbour) tends to chain, complete linkage gives compact groups, average linkage (UPGMA) is intermediate, and Ward's method minimises within-group variance. Non-hierarchical k-means partitions sites into a chosen number of groups. Divisive methods such as two-way indicator species analysis (TWINSPAN) split sites successively using indicator species and were widely used in vegetation classification. Indicator species analysis (IndVal) combines a species' specificity to a group (its relative abundance there) and fidelity (its frequency within the group) to identify characteristic species of each habitat or treatment. Hypothesis tests for multivariate data mostly use permutation, which avoids distributional assumptions. Permutational multivariate analysis of variance (PERMANOVA), introduced by Anderson (2001), partitions a distance matrix among factors much like ANOVA and computes a pseudo-F, with significance obtained by permuting observations; it is sensitive to differences in dispersion (spread) between groups as well as location, so a test of homogeneity of multivariate dispersion (PERMDISP) is run alongside. The analysis of similarities (ANOSIM) compares ranked distances between and within groups through an R statistic from about −1 to 1, with values near 0 indicating no difference. The Mantel test correlates two distance matrices, for example community dissimilarity and geographic distance, to test distance decay. Choices that matter as much as the method include transformation (square-root or log to downweight dominant species, Hellinger transformation before linear methods), treatment of rare species, standardisation for sampling effort, and reporting of the number of permutations. Multivariate results should be interpreted with the raw data: an ordination is a summary, not a test.
Tobler's first law of geography states that everything is related to everything else, but near things are more related than distant things. Spatial autocorrelation is the statistical expression of this: values at nearby locations are more similar (positive) or more dissimilar (negative) than expected by chance. It is both a nuisance and a signal. As a nuisance, it means that nearby samples carry overlapping information, so the effective sample size is smaller than the number of samples and standard tests have inflated Type I error. As a signal, it reveals the scale of processes such as dispersal, disturbance and soil formation. Global Moran's I ranges roughly from −1 to +1; values above its expected value under no autocorrelation, −1/(n − 1), indicate positive autocorrelation. Geary's c ranges from 0 to about 2, with 1 indicating no autocorrelation and values below 1 indicating positive autocorrelation. Local indicators of spatial association (local Moran's I, Getis–Ord Gi*) identify hot spots and cold spots. Correlograms plot autocorrelation against distance class. Point pattern analysis studies the locations of events such as trees, nests or pollution incidents. The Clark–Evans nearest-neighbour ratio is R = observed mean nearest-neighbour distance / expected distance, with the expected distance under complete spatial randomness equal to 0.5 / √density; R below 1 indicates clustering, about 1 randomness and above 1 regularity (maximum about 2.15 for a perfect hexagonal pattern). For example, trees at 0.01 per m² have an expected nearest-neighbour distance of 0.5 / 0.1 = 5 m; an observed mean of 3 m gives R = 0.6, a clustered pattern. Ripley's K function and its transformation L examine pattern across many distances simultaneously, with edge corrections and simulation envelopes. For quadrat counts, the variance-to-mean ratio is near 1 for a random (Poisson) pattern, above 1 for clumped and below 1 for regular patterns.
Geostatistics, developed in mining by Krige and Matheron, treats a continuous variable such as soil carbon, groundwater nitrate or rainfall as a realisation of a spatial random field. The semivariogram, γ(h) = half the mean squared difference between pairs of points separated by distance h, describes how dissimilarity grows with distance. Three parameters summarise it: the nugget (the semivariance at near-zero distance, combining measurement error and variation at scales smaller than the sampling interval), the sill (the plateau reached when points are no longer correlated) and the range (the distance at which the sill is reached, beyond which samples are effectively independent). The ratio of nugget to sill indicates spatial dependence; a widely used classification treats a nugget-to-sill ratio below 25 percent as strong, 25 to 75 percent as moderate and above 75 percent as weak. Models such as spherical, exponential and Gaussian are fitted to the empirical semivariogram. Kriging uses the fitted model to predict values at unsampled locations as weighted averages of nearby samples, with weights that minimise the prediction variance; it is the best linear unbiased predictor under its assumptions and also provides a kriging variance map, which can guide additional sampling. Ordinary kriging assumes an unknown constant mean; universal kriging or regression kriging models a trend with covariates; co-kriging uses a correlated, densely sampled secondary variable; indicator kriging estimates probabilities of exceeding thresholds, useful for contamination. Sampling designs for geostatistics need enough pairs at short distances to estimate the nugget and range, often by nested or cluster sampling. When the aim is to explain a response with predictors, spatial regression models account for autocorrelation in residuals: simultaneous and conditional autoregressive models, generalised least squares with spatial correlation structures, spatial random effects in mixed models, and geographically weighted regression, which lets coefficients vary over space. Ignoring residual autocorrelation can make weak predictors look significant.
Many sustainability questions concern people: why farmers adopt or abandon a practice, how communities govern a forest, how officials interpret a regulation. Qualitative research answers them by exploring meanings, perspectives and processes in depth rather than measuring frequencies. Common data collection methods are interviews (structured, with fixed questions; semi-structured, with a guide and freedom to probe; and unstructured, conversational), focus group discussions with typically six to ten participants guided by a moderator, participant observation and ethnography, in which the researcher spends extended time in the setting, and analysis of documents, media and archives. Sampling is purposive: participants are chosen for their relevance to the question, including key informants with specialist knowledge; snowball sampling uses participants to recruit others, useful for hard-to-reach groups; theoretical sampling selects new cases to develop emerging concepts. Sample size is usually decided by saturation, the point at which new data add no new themes. Analysis involves transcription, coding (labelling segments of text), grouping codes into categories and themes, and interpretation. Thematic analysis, as described by Braun and Clarke, is a flexible method for identifying patterns; grounded theory, from Glaser and Strauss, builds theory inductively through constant comparison; content analysis counts and categorises text; discourse analysis examines how language constructs issues. Quality is judged by trustworthiness criteria proposed by Lincoln and Guba: credibility (for example by member checking and prolonged engagement), transferability (thick description), dependability (an audit trail) and confirmability. Triangulation, the use of multiple data sources, methods, investigators or theories, strengthens findings. Reflexivity requires researchers to state how their own position and assumptions shape the research.
Participatory approaches involve local people as partners in producing knowledge rather than as subjects. Participatory rural appraisal (PRA), developed from rapid rural appraisal in the 1980s and 1990s and associated with Robert Chambers, uses visual and group tools that do not depend on literacy: resource and social mapping, transect walks with residents, seasonal calendars of rainfall, labour and food availability, historical timelines, Venn (institutional) diagrams of organisations and their importance, wealth ranking, and pairwise or matrix ranking of problems and options. Participatory action research cycles between joint inquiry and action. Participatory GIS lets communities map land use, sacred sites and customary boundaries, with uses in tenure claims and land-use planning. Citizen science engages volunteers in data collection or analysis. Participatory methods are open to dominance by powerful voices, so facilitators separate groups by gender, age or wealth where appropriate. When working with indigenous peoples and local communities, free, prior and informed consent and respect for traditional knowledge and its ownership are required. Surveys bridge qualitative and quantitative work: questionnaires with closed questions, Likert scales (typically five or seven points from strongly disagree to strongly agree) and open questions; they need pilot testing, careful translation and attention to response bias and non-response. Q methodology studies shared viewpoints by having participants rank statements. Mixed-methods research integrates qualitative and quantitative strands deliberately. In a convergent design both are collected in parallel and compared; in an explanatory sequential design a quantitative survey is followed by qualitative interviews to explain its results; in an exploratory sequential design qualitative work comes first to develop concepts or a survey instrument that is then tested quantitatively. Integration, in design, analysis and interpretation, is what distinguishes mixed methods from two separate studies.
A traditional narrative review summarises literature selected by the author and is vulnerable to selection bias. A systematic review answers a defined question using explicit, reproducible methods to find, select, appraise and synthesise all relevant evidence. The Collaboration for Environmental Evidence (CEE) publishes guidelines for systematic reviews and systematic maps in environmental management; reporting follows the PRISMA 2020 statement (a 27-item checklist and a flow diagram showing records identified, screened, excluded and included) or the ROSES standards designed for environmental evidence. The main steps are: frame the question (PICO or PECO); publish a protocol in advance, so that methods cannot be changed after seeing results; search several bibliographic databases with documented search strings, plus grey literature such as government reports and theses, in relevant languages; screen titles, abstracts and full texts against predefined eligibility criteria, ideally by two reviewers with agreement checked; appraise the validity of each study (risk of bias from design, confounding, selection and reporting); extract data with a tested form; and synthesise narratively, quantitatively or both. A systematic map catalogues the evidence base on a broad topic without synthesising effects, identifying gaps and clusters. Rapid reviews streamline steps for urgent policy questions and must state their shortcuts. Vote counting, tallying significant and non-significant studies, is discouraged because it ignores effect size and precision and is biased against small studies with low power.
Meta-analysis combines quantitative results from independent studies. Each study's result is expressed as an effect size with a variance. Common effect sizes in environmental science are the log response ratio, lnRR = ln(X̄T / X̄C), the logarithm of the treatment mean divided by the control mean, with variance approximately SDT²/(nT X̄T²) + SDC²/(nC X̄C²); the standardised mean difference (Hedges' g, Cohen's d corrected for small samples); the log odds ratio for binary outcomes; and Fisher's z transformation of correlation coefficients. A response ratio is back-transformed to a percentage change as (e^lnRR − 1) × 100; a treatment yield of 6.0 t ha⁻¹ against a control of 5.0 gives lnRR = ln 1.2 = 0.182, a 20 percent increase. Studies are weighted by the inverse of their variance, so precise studies count more. A fixed-effect (common-effect) model assumes one true effect shared by all studies; a random-effects model assumes true effects vary among studies with between-study variance τ², estimated by methods such as DerSimonian–Laird or REML, and is usually more appropriate for ecological data from different sites and conditions. Heterogeneity is tested with Cochran's Q, compared with a chi-square distribution on k − 1 degrees of freedom for k studies, and quantified with I² = (Q − df) / Q × 100 percent, the share of variation due to real differences rather than chance; Higgins and colleagues suggested 25, 50 and 75 percent as low, moderate and high. Meta-regression and subgroup analysis explain heterogeneity with moderators such as climate, soil or study duration. Non-independence, when one study contributes several effect sizes, is handled by multilevel models. Publication bias, the tendency for significant results to be published more readily, is explored with funnel plots (asymmetry suggests missing small non-significant studies), Egger's regression test, trim-and-fill and fail-safe numbers, none of which is conclusive. Sensitivity analyses check whether conclusions depend on a few studies or on quality.
Reproducibility means obtaining the same results from the same data and code; replicability means obtaining consistent results from new data collected to answer the same question. Large replication projects in several fields have found that many published findings do not replicate, prompting reforms. Questionable research practices include p-hacking (trying analyses until p falls below 0.05), HARKing (hypothesising after the results are known and presenting the hypothesis as prior), selective reporting of outcomes, and the garden of forking paths, in which many undisclosed analytic choices inflate false positives even without deliberate fishing. The American Statistical Association's 2016 statement on p-values warned that p-values do not measure the probability that a hypothesis is true or the size of an effect, and that scientific conclusions should not rest only on whether p passes a threshold; effect sizes with confidence intervals are preferred. Remedies include preregistration of hypotheses and analysis plans, registered reports (articles accepted on the basis of the question and methods before results are known), power analysis, and full reporting. Open data practice follows the FAIR principles (Wilkinson and colleagues, 2016): data should be Findable (persistent identifiers such as DOIs, rich metadata), Accessible (retrievable by standard protocols), Interoperable (standard formats and vocabularies) and Reusable (clear licence and provenance). The CARE principles for Indigenous data governance complement FAIR: Collective benefit, Authority to control, Responsibility and Ethics. A data management plan, now required by many funders, describes data types, formats, metadata standards (such as the Ecological Metadata Language), storage, backup, sharing, licences (for example CC BY or CC0) and long-term preservation in a trusted repository. Analysis code should be written as scripts, kept under version control, documented and archived with the data; computational environments can be recorded so that results can be rerun.
Research ethics covers integrity, treatment of people and animals, and responsibilities to the environment and communities. Research misconduct is defined in most codes as fabrication (making up data), falsification (manipulating data, materials or processes) and plagiarism (using others' words or ideas without credit), abbreviated FFP; it excludes honest error and differences of opinion. Related unacceptable practices include duplicate publication, salami slicing of one study into minimal publishable units, citation manipulation, undisclosed conflicts of interest and gift or ghost authorship. Widely used authorship criteria, from the International Committee of Medical Journal Editors, require substantial contribution to conception, data or analysis; drafting or critically revising the work; approval of the final version; and agreement to be accountable for it; other contributors are acknowledged. The CRediT taxonomy describes fourteen contributor roles. Research with people requires review by an ethics committee (institutional review board), voluntary informed consent, the right to withdraw, protection of privacy through anonymisation and secure storage, and special care with vulnerable groups. Research with animals follows the 3Rs of Russell and Burch: Replacement (use alternatives where possible), Reduction (use the fewest animals consistent with valid results, aided by power analysis) and Refinement (minimise pain and distress), with approval from an animal ethics committee. Field research needs permits for protected areas and collection, minimises disturbance, and follows the Nagoya Protocol on access and benefit-sharing (adopted 2010, in force 2014) when using genetic resources and associated traditional knowledge, and CITES rules for moving specimens of listed species across borders. Researchers should return results to the communities involved, respect data sovereignty and avoid predatory journals that charge fees without real peer review. Institutions and journals have policies for investigating allegations; the Committee on Publication Ethics provides guidance to editors.
Most research articles follow the IMRaD structure: Introduction (what is known, the gap, the question or hypotheses), Methods (enough detail for replication: site, design, sampling, measurements, statistical analysis and software), Results (findings in logical order with figures and tables, without interpretation) and Discussion (interpretation, comparison with other work, limitations, implications and future research). The title should state the main finding or question in specific terms; the abstract, usually 150 to 300 words, summarises background, aim, methods, key results with numbers and the main conclusion, and is often structured by headings; keywords aid indexing. Results should report effect sizes with confidence intervals and exact p-values rather than only stars, and give sample sizes for every estimate. Figures should be readable without the text, with labelled axes and units, error bars defined in the caption and colour schemes accessible to colour-blind readers. A thesis expands the same structure, typically with a literature review chapter and several research chapters, a general discussion, and appendices. References follow a citation style: author–date systems such as Harvard or APA cite (Author, year) in the text and list references alphabetically; numbered systems such as Vancouver cite by number in order of appearance. A bibliography may include works consulted but not cited, whereas a reference list includes only cited works. Footnotes and endnotes are used in some disciplines. Plain, precise writing is preferred: active voice where it clarifies who did what, defined abbreviations, consistent terms and SI units. Reference managers keep citations consistent, and similarity-checking software is used by journals and universities to detect plagiarism, though its scores need human interpretation.
Peer review is the evaluation of a manuscript by independent experts before publication. In single-anonymous (single-blind) review, reviewers know the authors' identities but not the reverse; in double-anonymous review neither knows the other; in open review identities and sometimes reports are published; post-publication review continues after publication through comments and replication. Editors decide to accept, request minor or major revision, or reject. Responding to reviewers requires a point-by-point reply that states how each comment was addressed or, politely and with evidence, why not. Reviewers should declare conflicts of interest, keep the manuscript confidential, judge the soundness of methods and conclusions, and write constructively. Preprints, posted before review on public servers, speed dissemination but must be read as unreviewed. Open access makes articles free to read, either through open journals, sometimes funded by article processing charges, or by depositing accepted manuscripts in repositories. Persistent identifiers, such as DOIs for articles and data and ORCID iDs for researchers, link outputs to people. Metrics are widely used and widely misused. The journal impact factor for a year is the number of citations in that year to items the journal published in the previous two years, divided by the number of citable items published in those two years; a journal with 600 citations in a year to 200 citable items from the two preceding years has an impact factor of 3.0. It describes journals, not individual articles or researchers, and citation distributions are highly skewed. The h-index of a researcher is the largest number h such that h of their papers have at least h citations each; it depends on career length and field. The San Francisco Declaration on Research Assessment (DORA, 2012) and the Leiden Manifesto urge assessing research on its own merits rather than journal metrics, and counting datasets, software and societal impact as outputs.
A student uses this subject to plan a first thesis that will survive examination: a clear question with rival hypotheses, a design whose experimental units are truly replicated, a power calculation that justifies the sample size, a data management plan and an analysis written as a script. In research-aptitude papers the same student must define action research, distinguish Type I and Type II errors, recognise plagiarism and predatory journals and compute an h-index. Common mistakes are treating subsamples as replicates, calling a non-significant result 'no effect', and choosing an ordination because the software offers it.
A practitioner five years into a consultancy, agency or NGO designs monitoring for environmental impact assessments and restoration projects, so the BACI design with several control sites and enough sampling dates before construction is a daily tool. Other decisions are how many permanent plots are needed to detect a 20 percent decline, when to use a mixed model for repeated surveys, how to run participatory mapping and focus groups that hear women and marginalised groups, and how to store data and code so that a regulator or certifier can audit the results.
A senior professional with twenty-five years of experience runs research programmes and long-term sites, sets institutional data and ethics policies and commissions evidence syntheses for policy. Judgements include whether a decades-old experiment should change its treatments, how to fund continuity of monitoring, when a rapid review is good enough for a ministerial decision, how to handle a misconduct allegation, and how to assess staff on the quality and use of their work rather than journal impact factors.
A researcher with a PhD and long experience shapes methods and standards: leading systematic reviews and meta-analyses that inform international assessments, developing designs and models for spatially and temporally correlated data, editing journals, chairing ethics committees, examining theses and supervising doctoral students. Such researchers also defend long-term experiments and archives, negotiate data sovereignty agreements with indigenous communities, and advise funders on reproducibility requirements, which means knowing the current debates on p-values, preregistration and open science.
This manual explains concepts and simple calculations; it does not teach statistical software, derive estimators, or cover Bayesian inference, structural equation modelling, causal inference methods beyond design (instrumental variables, matching), species distribution modelling or occupancy and capture–recapture models, all of which are important in environmental research. Rules of thumb quoted (NMDS stress, DCA gradient length, nugget-to-sill classes, I² bands, five levels for a random effect) are conventions, not laws, and are debated. Ethics approval procedures and permits differ by country and institution and must be checked locally.
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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