Forestry & Forest Sciences · Postgraduate & Professional Practice · also Research Methodology, Experimental Designs in Forestry, Advanced Biometry
Designing and analysing forestry research: field experiments with long-lived trees, advanced designs, mixed models, long-term plots and scientific writing.
In the exams: ICAR AICE-JRF 59 (PhD level across units); ICAR AICE-JRF Part A; ASRB NET and ARS recruitment
Forestry research has a problem that few other fields share: its subjects outlive its researchers. A spacing trial, a provenance test or a thinning experiment may run for forty years or more, through several generations of scientists, changes of funding and changes of measuring equipment, and a design flaw made in the first year cannot be corrected later. Trees are also large, variable and spread over heterogeneous ground, so experiments need big plots, borders, careful blocking and statistical models that handle repeated measurements on the same trees. This subject teaches how to plan, run, analyse and report forestry research so that the results are valid and useful to others.
The manual starts with the scientific method and the formulation of a research problem, including replication and statistical power. It then covers field experiments with trees (plot size, borders, replication and layout), factorial, split-plot and incomplete block designs, mixed-effects models and repeated measures, multivariate methods (principal components, cluster analysis and ordination), long-term experiments and permanent sample plots, meta-analysis and systematic reviews, research ethics, data management and reproducible analysis, and scientific writing, peer review and research proposals. Elementary statistics, sampling and basic analysis of variance are taught in the biometry and inventory subjects of this track and are assumed here.
Doctoral fellowship and research-service examinations in agricultural and forestry sciences test this material across subjects: designing an experiment for a stated objective, choosing a design and computing its degrees of freedom, identifying pseudoreplication, interpreting variance components and ordination output, defining meta-analytic quantities, and knowing the rules of research ethics. Short numericals include sample size from a power calculation, degrees of freedom of a split-plot design, coefficients of variation, intraclass correlation, the share of variance in a principal component, growth and mortality rates from remeasured plots, effect sizes and heterogeneity statistics.
Research begins with a problem: a gap in knowledge or a practical difficulty, such as poor survival of a planted species on degraded soils or uncertainty about how thinning affects drought resistance. A good research problem is specific, important to someone, and answerable with the time, money and methods available. It is refined through a literature review that establishes what is already known, which methods have worked and where the evidence is weak. The problem is then stated as objectives and, where possible, as testable hypotheses. A scientific hypothesis is a provisional explanation that makes predictions which could be shown false by observation; the philosopher Karl Popper argued that falsifiability is what separates scientific statements from others. In statistics the null hypothesis (H₀) usually states no effect or no difference, and the alternative (H₁) states the effect the researcher expects; the test asks whether the data are improbable under H₀.
Science uses both deduction, deriving predictions from a general theory, and induction, generalising from observed cases; most research cycles between them. Research may be descriptive (what exists, such as an inventory of a forest type), correlative or observational (how variables co-vary, such as growth versus soil depth across sites), or experimental (what happens when the researcher manipulates a factor, such as fertiliser rate). Only manipulative experiments with randomisation can establish cause and effect with confidence, because randomisation breaks the link between treatment and unmeasured confounding variables. Observational studies are often the only option at large scales or long time spans, such as studies of climate effects on growth, and their causal claims must be argued carefully, controlling for confounders and using natural experiments where they exist.
The experimental unit is the smallest unit to which a treatment is independently applied: a plot that receives a fertiliser treatment, a seedling in a pot, a stand that is burned. The observational unit is what is measured, which may be smaller, such as individual trees within the plot. Replication means applying each treatment to several independent experimental units; it gives an estimate of experimental error, increases precision and allows generalisation. Measuring many trees in one plot gives subsampling, not replication. Hurlbert in 1984 named the error of treating subsamples or repeated measurements as if they were independent replicates pseudoreplication; it inflates the apparent precision and gives false significant results. A classic forestry example is applying a burning treatment to one large stand and an unburned control to another, and then testing the difference using the many trees in each stand: the stands, not the trees, are the experimental units, and with one stand per treatment there is no valid estimate of error for the treatment effect.
The three basic principles of experimental design, set out by R. A. Fisher, are replication, randomisation (assigning treatments to units by chance so that no systematic bias enters) and local control (blocking or other means of reducing error by grouping similar units).
Statistical power is the probability that a test detects an effect of a given size when it exists; it is 1 − β, where β is the probability of a type II error (missing a real effect). The type I error rate α is the probability of declaring an effect when none exists, commonly set at 0.05. Power depends on α, the size of the effect, the variability of the response and the number of replicates. Before an experiment, a power analysis estimates the number of replicates needed. For comparing two means with equal replication, an approximate formula is n per group ≈ 2(z₁₋α/₂ + z₁₋β)² σ² ÷ δ², where σ is the standard deviation of the response and δ the smallest difference worth detecting. With σ = 4 cm of height growth, δ = 3 cm, α = 0.05 (z = 1.96) and power 0.80 (z = 0.84), n ≈ 2 × 2.80² × 16 ÷ 9 ≈ 27.9, so 28 units per treatment are needed. The variance estimate usually comes from a pilot study or earlier experiments. An underpowered study wastes resources, because a non-significant result cannot distinguish "no effect" from "too few replicates".
Forest field experiments need plots large enough to represent a stand and to survive the loss of some trees, but small enough to fit many replicates on uniform ground. Plot size depends on the treatment and the age to which the trial will run: a fertiliser or spacing trial intended to reach rotation age needs plots holding enough trees at the end, after mortality and thinning, often 25 to 50 measured trees or more, while a short nursery or early-survival trial can use far smaller units. Square or nearly square plots have the smallest perimeter for their area and therefore the smallest edge effects; long narrow plots follow gradients poorly unless the long side runs along the contours of variation.
Trees at the edge of a plot compete with trees of the neighbouring plot, which may have a different treatment. If a heavily fertilised or widely spaced plot lies next to an untreated or dense one, edge trees respond to their neighbours as well as to their own treatment. This inter-plot competition is controlled by surrounding the measured (net) plot with one or more border or buffer rows that receive the same treatment but are not measured. In a gross plot of 6 × 6 trees with a single border row, only the inner 4 × 4 = 16 trees are measured, 44% of those planted, which shows why borders are expensive and why trials of treatments that strongly change tree size need wide borders. Root trenching is sometimes used where roots cross plot boundaries, as in nutrient and water studies.
Forest sites vary in soil depth, drainage, slope, aspect and previous land use, often over short distances. Uniformity trials, in which one treatment is applied to a whole area and yields are recorded in small units, show how variance changes with plot size. H. Fairfield Smith's empirical law expresses this as Vₓ = V₁ ÷ xᵇ, where Vₓ is the variance per unit area of plots of x basic units, V₁ the variance of single units, and b a soil heterogeneity index between 0 and 1; b close to 1 means neighbouring units are nearly independent, so many small plots are efficient, while b close to 0 means strong correlation between neighbours, so larger plots do little to reduce variance. Blocking groups plots that are similar, such as plots along the same contour or the same soil type, so that each block contains every treatment and differences between blocks are removed from the error. Blocks should be as compact as possible and oriented so that variation is between rather than within blocks.
Randomisation within blocks is done by a documented random procedure, and the field layout is mapped and permanently marked. Records include the randomisation, plot coordinates, the seedlots or clones used and planting dates. Unequal survival and missing trees are common; the analysis must use plot means or models that account for the number of trees, and replacement planting of dead trees in the first season is often allowed only with replacements of the same seedlot and recorded.
Genetic tests of families, clones and provenances often use many entries, so block size becomes a problem: a complete block containing every one of 200 families in multi-tree plots would be large and heterogeneous. Two responses are single-tree plots, in which each family is represented by one tree per block and many blocks are used, which gives small, homogeneous blocks and efficient estimates of genetic parameters but is vulnerable to mortality and unsuited to stand-level traits; and incomplete block designs, discussed in the next chapter. Spacing experiments can use systematic designs such as the Nelder fan or wheel, in which spacing changes progressively along spokes, saving area at the cost of formal randomisation. Long-term trials must also plan for future thinning, which itself changes the treatments, and for the eventual felling and wood-quality measurements. Because results take decades, experiments are often established as networks across several sites, so that treatment-by-site interactions can be estimated and conclusions generalised.
A factorial experiment tests two or more factors together, using every combination of their levels, so that interactions can be estimated. An interaction exists when the effect of one factor depends on the level of another, as when fertiliser increases growth at wide spacing but not at close spacing. Factorial designs are efficient because every unit contributes to the estimate of every main effect. A 2³ factorial (three factors at two levels each) has 8 treatment combinations; a 3 × 4 factorial has 12. In a randomised complete block design (RCBD) with t treatments and r blocks, the error degrees of freedom are (t − 1)(r − 1); a 3 × 4 factorial in four blocks therefore has 12 − 1 = 11 treatment degrees of freedom (2 for the first factor, 3 for the second and 6 for the interaction) and (12 − 1)(4 − 1) = 33 error degrees of freedom.
The coefficient of variation, CV = √(error mean square) ÷ general mean × 100, summarises experimental precision: an error mean square of 16 with a mean of 40 gives a CV of 10%. The standard error of a difference between two treatment means each based on r replicates is √(2 × EMS ÷ r); with EMS = 16 and r = 4 it is √8 ≈ 2.83. When factors are quantitative, such as fertiliser rates or spacing, response curves (linear and quadratic contrasts or regression) are more informative than pairwise comparisons. When interaction is significant, main effects can mislead and simple effects (the effect of one factor at each level of the other) should be reported.
When one factor is hard or costly to apply to small plots, such as site preparation by machine, irrigation or prescribed burning, it is applied to large main plots, and a second factor that can be applied to small units, such as species, clones or fertiliser, is randomised to subplots within each main plot. This is the split-plot design. It has two error terms: main-plot error, used to test the main-plot factor, and subplot error, used to test the subplot factor and the interaction. Because main plots are fewer and larger, the main-plot factor is estimated less precisely. For a split-plot in an RCBD with r blocks, a main-plot levels and b subplot levels, the degrees of freedom are: blocks r − 1, main factor a − 1, main-plot error (r − 1)(a − 1), subplot factor b − 1, interaction (a − 1)(b − 1), and subplot error a(r − 1)(b − 1). With r = 4, a = 3 and b = 4 these are 3, 2, 6, 3, 6 and 27, summing to the total of rab − 1 = 47. Testing the main-plot factor against the subplot error is a common and serious mistake that exaggerates significance.
In a strip-plot (strip-block) design, both factors are applied in strips, one horizontal and one vertical, across each block, which suits two factors that both need large areas, such as tillage and row direction; it has three error terms. Split-split-plot designs add a third level of splitting.
When the number of treatments is too large for every block to contain them all, incomplete block designs place only some treatments in each block, arranged so that comparisons remain balanced or nearly so. In a balanced incomplete block design (BIBD) with t treatments, b blocks of size k and r replicates, each pair of treatments occurs together in the same number λ of blocks, and the parameters satisfy bk = tr and λ(t − 1) = r(k − 1). With t = 7, k = 3 and r = 3, b = 7 × 3 ÷ 3 = 7 and λ = 3 × 2 ÷ 6 = 1. BIBDs exist only for certain combinations of parameters. Lattice designs, in which the number of treatments is a perfect square, and especially alpha designs (alpha-lattices), developed by Patterson and Williams in 1976, are flexible resolvable incomplete block designs: the incomplete blocks group into complete replicates, so the trial can be analysed as an RCBD if block effects prove small. Alpha designs are widely used in tree breeding trials with many families or clones. Analysis recovers inter-block information by treating incomplete blocks as random effects in a mixed model. Row–column designs extend the idea by blocking in two directions, useful on sites with gradients across and along the slope.
Forestry data are hierarchical: trees within plots, plots within blocks, blocks within sites, and repeated measurements on the same trees over time. Mixed-effects models handle this structure by combining fixed effects, whose specific levels are of interest and would be repeated in a new study (treatments, fertiliser rates, species chosen for comparison), with random effects, whose levels are a sample from a larger population and are of interest mainly through their variance (blocks, sites, families in a breeding population, individual trees). Random effects induce correlation among observations that share a level: two trees in the same plot are more alike than two trees in different plots. Ignoring this correlation by fitting an ordinary regression to all trees is a form of pseudoreplication and understates standard errors.
The share of variance due to a grouping level is the intraclass correlation, ICC = σ²_group ÷ (σ²_group + σ²_residual). With a plot variance component of 6 and a residual (tree) variance of 18, ICC = 6 ÷ 24 = 0.25: a quarter of the variation among trees is between plots. Variance components are estimated by restricted maximum likelihood (REML), which accounts for the degrees of freedom used in estimating the fixed effects and gives less biased variance estimates than ordinary maximum likelihood (ML), especially in small samples. Predicted values of random effects are best linear unbiased predictions (BLUPs), which shrink extreme group means towards the overall mean in proportion to their uncertainty; BLUPs of family or clone effects are the basis of breeding values in tree improvement.
Measuring the same trees or plots repeatedly over time produces repeated measures, which are correlated, usually more strongly for measurements close in time. The classical repeated-measures analysis of variance assumes sphericity (equal variances of all pairwise differences between times); when it is violated, the Greenhouse–Geisser or Huynh–Feldt corrections reduce the degrees of freedom. Mixed models offer more flexibility by modelling the covariance among repeated measurements directly. Common structures are compound symmetry (equal correlation between all pairs of times), first-order autoregressive, AR(1), in which the correlation between times k steps apart is ρᵏ, and unstructured, which estimates every variance and covariance separately and needs many parameters. Unequally spaced measurements can be handled by spatial-power or continuous-time autoregressive structures.
Growth curves are often modelled with random intercepts and random slopes for each tree or plot, allowing each to have its own starting size and growth rate around the population average; nonlinear mixed models fit sigmoid growth functions such as the Chapman–Richards or logistic, with random effects on asymptote or rate parameters. Missing measurements, common in long-term trials, are handled naturally by likelihood-based mixed models provided the data are missing at random.
Competing models are compared with likelihood ratio tests for nested models or with information criteria. Akaike's information criterion, AIC = 2k − 2 ln L, where k is the number of parameters and L the maximised likelihood, penalises complexity; the model with the lowest AIC is preferred, and differences of less than about 2 indicate little support for one over the other. Models that differ in their fixed effects must be compared using ML, not REML, because REML likelihoods depend on the fixed-effect structure; models differing only in random effects can be compared using REML. Residuals are checked for normality, constant variance and remaining patterns against fitted values, time and space; a variance that grows with tree size is common and is handled by modelling the variance as a function of the mean or by transforming the response. Spatial correlation among neighbouring plots or trees in field trials can be modelled with row–column autoregressive structures, a standard step in analysing large tree breeding trials.
Many forestry datasets have several correlated variables per unit: growth, form, wood density and branch traits of clones; soil chemistry of plots; abundance of many species at many sites. Multivariate methods summarise such data. Principal component analysis (PCA) finds new uncorrelated variables, principal components, that are linear combinations of the original variables and capture as much of the variance as possible in order: the first component the most, the second the most of what remains, and so on. Components are the eigenvectors of the covariance or correlation matrix, and their eigenvalues are the variances they explain. When variables are in different units (centimetres, grams per cubic centimetre, counts), PCA is done on the correlation matrix, which standardises each variable to unit variance; the eigenvalues then sum to the number of variables p, so a first eigenvalue of 2.7 from six variables explains 2.7 ÷ 6 = 45% of the total variance. The Kaiser criterion retains components with eigenvalues greater than 1, and a scree plot shows where additional components add little. Loadings (correlations between variables and components) are used to interpret what each component represents, such as a general size axis or a contrast between growth and wood density.
Cluster analysis groups units so that members of a group are more similar to one another than to members of other groups. It starts from a measure of distance or dissimilarity between every pair of units. Euclidean distance suits continuous variables on comparable scales, usually after standardisation. For species abundance data, Euclidean distance behaves poorly because two sites sharing no species can appear similar if both have low abundances; the Bray–Curtis dissimilarity, BC = 1 − 2C ÷ (S₁ + S₂), where C is the sum of the lesser abundances of each species shared by the two sites and S₁ and S₂ are the total abundances at each site, is preferred. For sites with abundances (10, 5, 0) and (6, 5, 3) of three species, C = 6 + 5 + 0 = 11, S₁ = 15, S₂ = 14, and BC = 1 − 22 ÷ 29 ≈ 0.24. Presence–absence data use indices such as Jaccard or Sørensen.
Hierarchical agglomerative clustering joins the two most similar units or groups at each step, producing a dendrogram. The linkage rule defines distance between groups: single linkage (nearest neighbour) tends to chain groups together; complete linkage (furthest neighbour) gives compact groups; average linkage (UPGMA) is intermediate; and Ward's method joins the groups whose merger least increases within-group variance. Non-hierarchical methods such as k-means partition units into a chosen number of groups. Clusters are a description of the data, not a test, and different choices of distance and linkage give different groupings, so results should be checked for stability.
Ordination arranges sites or species along a few axes so that similar units lie close together, revealing gradients in community composition. Unconstrained (indirect) ordination methods use only the community data: PCA assumes linear responses of species to gradients and is suited to short gradients; correspondence analysis (CA) assumes unimodal responses, typical of species along long environmental gradients, but can produce an arch effect in which the second axis is a curved function of the first; detrended correspondence analysis (DCA) removes the arch artificially. Non-metric multidimensional scaling (NMDS) places units so that rank order of distances in the ordination matches rank order of the original dissimilarities (often Bray–Curtis) as closely as possible; its fit is measured by stress, with values below about 0.1 regarded as good and above about 0.2 as poor. Constrained (direct) ordination, such as redundancy analysis (RDA, linear) and canonical correspondence analysis (CCA, unimodal), finds axes that are combinations of measured environmental variables and tests how much community variation they explain. Differences in composition among groups, such as treatments, are tested by permutational multivariate analysis of variance (PERMANOVA) on a dissimilarity matrix, which makes no assumption of multivariate normality.
Some of the most valuable knowledge in forestry comes from plots measured for decades. Long-term thinning and spacing trials, many established in Europe in the nineteenth and early twentieth centuries and later across the world, provided the data for yield tables and growth models. Permanent sample plots (PSPs) in natural forests show rates of growth, mortality and recruitment, the response of forests to climate and disturbance, and the dynamics of species composition. International networks, such as large forest dynamics plots of tens of hectares in which every stem above 1 cm diameter is mapped and remeasured, networks of tropical forest plots across the Amazon, Africa and Asia, and transnational monitoring of forest condition in Europe, have revealed long-term changes in carbon storage and tree mortality that no short study could detect. National forest inventories increasingly use permanent rather than temporary plots, because remeasurement of the same plots estimates change much more precisely than comparison of independent samples.
The value of long-term data depends on consistent methods. Changing the measurement height of diameter, the minimum diameter, the plot size or the definition of a living tree midway through a series creates artificial changes. Protocols therefore fix these definitions, mark the point of diameter measurement with paint or a nail, tag each tree with a unique number, map tree positions, and record any necessary change in method together with a period of overlap in which old and new methods are both used.
Remeasured plots allow components of change to be separated. Following the definitions of Beers, with V₁ and V₂ the volumes of live trees at the first and second measurements, M the volume of trees that died, C the volume cut, and I the volume of ingrowth (trees crossing the minimum size), gross growth including ingrowth is V₂ + M + C − V₁, net growth including ingrowth is V₂ + C − V₁, and net increase is V₂ − V₁. For example, if live volume rises from 180 to 220 m³ per ha in five years, with 12 m³ per ha of mortality and no cutting, gross growth is 220 + 12 − 180 = 52 m³ per ha, or a periodic annual increment of 10.4 m³ per ha per year, while net growth is 40 m³ per ha, 8.0 m³ per ha per year.
Annual mortality rates in tree populations are calculated with a compound formula that accounts for the interval: m = 1 − (N_s ÷ N₀)^(1/t), where N₀ is the initial number of trees, N_s the survivors and t the interval in years. If 450 of 500 trees survive five years, m = 1 − 0.9^0.2 ≈ 0.021, or 2.1% per year, slightly more than the simple 10% ÷ 5 = 2.0%. Recruitment rates are calculated similarly. Rates from intervals of different length are not directly comparable without such corrections, because some trees recruit and die between censuses unseen.
Long-term research needs institutional commitment beyond any one project: secure land tenure, legal protection of plots from harvesting or encroachment, permanent marking that survives fire and decades, budgets for remeasurement, and archives that keep data and metadata usable after the original researchers have left. Field manuals describe procedures in enough detail for new staff to repeat them. Data are checked at each remeasurement against previous values, so that a tree that shrinks implausibly or a dead tree that comes back to life is investigated while it can still be checked in the field. Sharing data through networks and open repositories multiplies their value, and co-authorship or acknowledgement policies recognise the people who maintained plots for decades.
A systematic review answers a defined question by finding, appraising and synthesising all relevant studies using explicit, reproducible methods, as opposed to a narrative review in which the author selects studies informally. The question is framed with its components, often summarised as population, intervention or exposure, comparator and outcome (PICO), for example: in tropical plantations (population), does mixing nitrogen-fixing trees with eucalypts (intervention) compared with eucalypt monocultures (comparator) change stand biomass (outcome)? A protocol, ideally registered in advance, sets the search strategy (databases, search strings, grey literature), inclusion and exclusion criteria, data to be extracted, critical appraisal of study quality and the synthesis method. Screening of titles, abstracts and full texts is often done by two reviewers independently. Reporting guidelines such as PRISMA set out the information a review should report, including a flow diagram of studies found, screened and included. Collaboration for Environmental Evidence guidelines adapt these methods to environmental management questions.
Meta-analysis is the statistical synthesis of results from several studies. Each study's result is converted to a common effect size with its sampling variance. Common effect sizes in ecology and forestry are the log response ratio, lnRR = ln(X̄_T ÷ X̄_C), the natural logarithm of the ratio of treatment to control means, which expresses proportional change (lnRR = ln(12 ÷ 10) ≈ 0.18, a 20% increase); the standardised mean difference, such as Hedges' g, which divides the difference by the pooled standard deviation with a small-sample correction; and correlation coefficients transformed by Fisher's z. Simply counting how many studies found significant effects (vote counting) is misleading, because it ignores effect size and study power.
Studies are pooled with inverse-variance weights, wᵢ = 1 ÷ vᵢ, so precise studies count more. In a fixed-effect (common-effect) model, all studies are assumed to estimate one true effect, and the pooled estimate is Σwᵢyᵢ ÷ Σwᵢ with standard error 1 ÷ √Σwᵢ. For two studies with effects 0.2 and 0.5 and variances 0.01 and 0.04, the weights are 100 and 25 and the pooled effect is (20 + 12.5) ÷ 125 = 0.26, with standard error 1 ÷ √125 ≈ 0.089. A random-effects model assumes the true effect varies among studies, adds the between-study variance τ² to each study's variance, and gives wider confidence intervals; it is usually more realistic for ecological data from different sites and species.
Heterogeneity among study results is tested with Cochran's Q, the weighted sum of squared deviations of study effects from the pooled effect, compared with a chi-square distribution with k − 1 degrees of freedom for k studies. The I² statistic, (Q − df) ÷ Q × 100%, estimates the percentage of variation due to real differences rather than chance: with Q = 40 from 20 studies (19 df), I² = 21 ÷ 40 = 52.5%, moderate heterogeneity. Heterogeneity is explored by subgroup analysis and meta-regression on study characteristics such as climate, species or stand age.
Publication bias arises when studies with significant or large effects are more likely to be published, inflating pooled effects. It is examined with funnel plots of effect size against precision, which should be symmetrical in the absence of bias, and with tests such as Egger's regression; including grey literature and theses reduces the problem. Sensitivity analyses check whether conclusions depend on a few influential studies or on studies of low quality. A meta-analysis is only as good as the studies it combines, and pooling studies of different quality or with incompatible definitions can give a precise-looking answer to an ill-posed question.
Research integrity rests on honesty in proposing, performing, reviewing and reporting research. The three forms of research misconduct recognised by most institutions and funders are fabrication (making up data), falsification (manipulating materials, equipment, processes or data, or omitting data, so that the record is misrepresented) and plagiarism (using others' ideas, words or results without credit). Questionable research practices that are less obvious but also damaging include selective reporting of favourable outcomes, testing many hypotheses and reporting only significant ones (p-hacking), presenting hypotheses formed after seeing the data as if they were planned (HARKing), and inappropriate authorship. Authorship should be limited to those who made substantial intellectual contributions and take responsibility for the work; contributor taxonomies such as CRediT describe each author's role. Conflicts of interest, such as funding from a company whose product is tested, must be declared.
Forestry research often requires permissions: research permits for protected areas; permits to collect and export specimens and genetic material, which under the Nagoya Protocol to the Convention on Biological Diversity involve prior informed consent of the provider country and agreed benefit-sharing; CITES permits for listed species; and animal ethics approval for work with wildlife. Research with people, such as household surveys on forest use, interviews with forest workers or participatory mapping, needs review by an ethics committee, informed consent, protection of confidentiality, and, where Indigenous peoples or local communities are involved, free, prior and informed consent and respect for their rights over traditional knowledge and data.
A data management plan, now required by many funders, sets out what data will be collected, in what formats, with what metadata, where they will be stored and backed up, who may access them, how long they will be kept and how they will be shared. Good practice keeps raw data unchanged in a read-only form, with all cleaning and corrections done by documented scripts so that every step from raw to analysed data can be repeated; uses consistent, documented variable names and units; records metadata on who collected the data, where, when, how and with what instruments; stores data in open, non-proprietary formats; and keeps several copies in different places. Field data entered on tablets or paper are checked for range errors, impossible values and inconsistencies with earlier measurements as soon as possible. Data are deposited in recognised repositories with persistent identifiers and clear licences, following the FAIR principles (findable, accessible, interoperable, reusable), with sensitive information such as locations of rare species or personal data protected.
An analysis is reproducible when another researcher, given the same data and code, obtains the same results; it is replicable when a new study, collecting new data, reaches the same conclusions. Scripted analysis in a statistical programming language, rather than undocumented point-and-click steps, together with version control, records of software versions and literate programming documents that combine code, results and text, makes analyses reproducible. Preregistration of hypotheses and analysis plans before data are examined guards against p-hacking and HARKing. When many tests are performed, the chance of at least one false positive rises; the Bonferroni correction tests each of m hypotheses at α ÷ m (for 10 tests at α = 0.05, each at 0.005), and less conservative methods control the false discovery rate. Reporting should give effect sizes with confidence intervals, not just p-values, and should state all analyses done, including those that gave non-significant results. A p-value is the probability, if the null hypothesis were true, of obtaining data at least as extreme as those observed; it is not the probability that the null hypothesis is true.
Most scientific papers follow the IMRaD structure: Introduction (the problem, what is known, the gap and the objectives or hypotheses), Methods (enough detail for another researcher to repeat the study: site, design, measurements, analysis and software), Results (what was found, presented in logical order with figures and tables, without interpretation), and Discussion (what the results mean, how they compare with other studies, their limitations and implications), followed by conclusions, acknowledgements, references and supplementary material. The title should state the main finding or subject specifically; the abstract, often the only part read, summarises the problem, methods, key results with numbers and the main conclusion in a few hundred words. Figures should show the data, with axes labelled with variables and units and with measures of uncertainty explained. Statistical reporting should state the test or model, the effect size and its confidence interval, the sample size and the experimental unit. Clear writing uses short sentences, defines terms and abbreviations on first use, and puts the important point at the start of each paragraph.
Choosing a journal involves its scope, audience, peer-review standards and open-access policy. Predatory journals, which charge publication fees but do not provide genuine peer review or editorial services, damage careers and the literature; warning signs include unsolicited invitations, promises of very rapid publication, false claims of indexing and impact factors, and editorial boards that cannot be verified. Journal-level metrics such as impact factors measure average citation of a journal, not the quality of an individual article, a point made by statements such as the San Francisco Declaration on Research Assessment (DORA).
Peer review is the evaluation of a manuscript or proposal by independent experts before publication or funding. In single-blind review the reviewers know the authors' identities but not vice versa; in double-blind review neither knows the other; in open review identities are disclosed and reports may be published. Reviewers assess whether the question is important, the methods sound, the analysis appropriate, the conclusions supported by the data and the presentation clear, and they must declare conflicts of interest and keep manuscripts confidential. Editors decide to accept, request minor or major revision, or reject. Authors respond to each reviewer comment point by point, explaining changes made or giving reasoned arguments where they disagree; politeness and completeness matter. Reviewing for journals is part of a researcher's professional duty and is a good way for early-career scientists to learn standards.
A research proposal persuades a funder that a question matters, that the approach will answer it, and that the team can deliver. Typical sections are a title and summary; background and justification, including the problem and the gap in knowledge; aims, objectives and hypotheses; methods, including design, sample sizes justified by power analysis, measurements and analysis; a work plan with milestones, often as a timeline chart; expected outputs, outcomes and impact, and how results will reach users; a data management plan; ethics and permits; risks and how they will be managed; the team and its capacity; and a budget with justification. Development and applied research funders often ask for a logical framework (logframe) linking activities to outputs, outcomes and goals, with indicators, means of verification and assumptions. Objectives should be specific, measurable, achievable, relevant and time-bound. Long-term forestry experiments need proposals that plan explicitly for how measurements will continue after the funded project ends.
A postgraduate student uses this subject to plan a thesis: framing a testable hypothesis, identifying the experimental unit, choosing between an RCBD, a split-plot or an alpha design, running a power analysis to justify replication, laying out plots with borders, and writing a proposal that a committee will approve. In analysis the student fits mixed models rather than treating trees as replicates, uses ordination for community data, keeps raw data read-only and analyses them by script, and writes chapters in IMRaD form. Examinations test definitions, degrees of freedom, CV and power calculations and the recognition of pseudoreplication in a described study.
A research forester five years into a career runs field trials and permanent plots for an institute or company: establishing new experiments with proper randomisation and marking, remeasuring old ones to consistent protocols, checking data against previous censuses, calculating growth, mortality and recruitment, and producing reports and papers. Typical decisions are how large plots and borders must be for a new spacing trial, whether a damaged replicate can still be analysed, which covariance structure fits repeated measurements, and how to respond to a sceptical journal reviewer. The same person often reviews proposals from colleagues and writes data management plans for grant applications.
A senior scientist or research manager with twenty-five years of experience sets the research agenda of a programme, decides which long-term experiments to continue, close or merge, secures land tenure and budgets for remeasurement, and enforces data standards and archiving so that decades of records remain usable. They review and approve designs before trials are planted, because design errors cannot be corrected later, handle cases of suspected misconduct or authorship disputes, negotiate data-sharing agreements with networks, and judge which evidence syntheses are reliable enough to inform policy and management guidelines.
A researcher with a PhD and long experience develops methods as well as using them: efficient designs for large breeding and multi-site trials, spatial and mixed models for long-term data, meta-analyses that synthesise global evidence on questions such as mixed plantations or thinning and drought, and protocols for international plot networks. Such researchers supervise doctoral students, examine theses and fellowship candidates, serve as journal editors and on funding panels and ethics committees, and are responsible for passing long-term experiments and their data intact to the next generation of scientists.
This manual explains designs and models and gives the standard formulas; it does not replace a statistics text or software manual, and it does not cover Bayesian methods, generalised linear mixed models for counts and proportions, structural equation models or spatial statistics in depth. Rules for ethics approval, permits and data protection differ by country and institution and must be checked locally. Thresholds such as NMDS stress values and AIC differences are conventions rather than strict rules.
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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