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A biological cell is a membrane-bounded basic unit of living organization. In a cell-level experiment it can be an experimental unit, provided that treatment assignment and relevant interactions are handled at that level.

The shared architecture of cellular life combines a selective cell membrane, internal cytoplasm, inherited information in DNA, and ribosomes that assemble proteins. Metabolism supplies transformations of matter and energy needed for maintenance and growth. These components form a coupled system: a boundary retains useful molecules, enzymes organize chemical reactions, and inherited information supports rebuilding the machinery. See Clark, Douglas and Choi, Biology 2e: prokaryotic cells.

A worked structural comparison: in a typical prokaryote, DNA occupies a region without a surrounding cell nucleus; in a typical nucleated eukaryote, much of the DNA lies inside a membrane-bounded cell nucleus. Both still have a cell membrane, cytoplasm and ribosomes. The extra boundary compartmentalizes processes; it does not create a different basic principle of living organization. See Clark, Douglas and Choi, Biology 2e: eukaryotic cells.

Shared architecture describes cellular life and its developmental machinery, rather than requiring every specialized biological cell to retain every component. A mature mammalian red blood cell, for example, lacks a cell nucleus, although it develops from nucleated precursors. See Clark, Douglas and Choi, Biology 2e: components of blood. This distinction makes cellular unity compatible with striking specialization.

A biological replicate repeats a procedure using a distinct biological preparation, such as another plant or a separately established cell culture. The relevant level must be specified: several cell cultures derived from one donor can still form nested measurements for a donor-level question. Calling a sample a biological replicate does not by itself establish an independent experimental unit.

A block design assigns treatments to experimental units partitioned into blocks. Its incidence counts $n_{ij}$ record how often treatment $i$ occurs in block $j$. Balance and connectedness determine which treatment contrasts are estimable and how much adjustment for blocks costs.

A block groups experimental units expected to have similar background responses. Comparing treatments within blocks can reduce the variance of an estimator. Block allocation must be specified before responses are used to evaluate treatment effects.

A completely randomized design assigns treatments directly to available experimental units using complete randomization, without blocking. Fixed group sizes can be enforced. The residual then includes uncontrolled between-unit variation.

Design of experiments chooses experimental units, treatments, replication, blocks in experimental design and randomization so that scientifically useful treatment contrasts can be estimated with meaningful standard errors. Allocation determines which measurements supply independent treatment information.

An experimental unit is a unit to which a treatment is assigned under the experimental allocation. A whole orchard can be an experimental unit even when responses are recorded separately on its trees. Different factors in a split-plot design can have different experimental units.

A specified test for germination, recording the endpoint, conditions and observation window. For a proposed red/far-red light test, use randomization to allocate one seed lot to darkness, red, red then far-red, and red then far-red then red. Match hydration, temperature, handling and elapsed time before counting; use sham waiting periods to equalize schedules. Use dish replication, retain the dark scientific control, and record radicle emergence using an observation procedure that does not itself provide an uncontrolled light treatment. This is a proposed design, not a claim about the 1952 paper's randomization or replication.

As an original hypothetical counting example, begin with $N=40$ seeds in one dish. Suppose 12 first meet the radicle endpoint by 24 hours, eight additional seeds by 48 hours, and four additional seeds by 72 hours. These invented event counts giveand cumulative sample proportions $\hat{G}(24)=0.30$, $\hat{G}(48)=0.50$ and $\hat{G}(72)=0.60$. The 48-hour increment is $8/40=0.20$, not $0.50$; the latter includes earlier events. Counting the same emerged radicle again at each inspection would inflate the total. These numbers illustrate bookkeeping, not biological rates or treatment effects.

With a fixed denominator and irreversible classification of the first endpoint event, the set counted at an earlier inspection is a subset of the set counted later. Hence $0\le \hat{G}(t)\le 1$ and $\hat{G}(t)$ cannot decrease. This short proof applies to cumulative germination counts even if a later seedling dies. A count of currently surviving seedlings has a different definition and can decrease.

For treatment comparisons, the dish may be the experimental unit: seeds in the same dish share conditions. Forty seeds in one dish do not supply forty independent dish replicates. Report the sample size, replication, endpoint time and denominator; a sample proportion by a deadline measures this assay's outcome, not an unconditional fraction with seed viability.

Nested measurements are responses grouped inside larger units, with each measured object belonging to just one such unit. Three leaves within each pot give nested measurements; repeatedly reading one leaf gives another level of repetition. Either can yield clustered data. A common random effect can describe the shared influence of the containing experimental unit.

For the constructed pot example, label treatments by $g\in \{A,B\}$, pots within each group by $i=1,\dots ,n$, and leaves within each pot by $j=1,\dots ,m$. Consider the statistical modelHere $Y_{gij}$ is a leaf length, $\mu +{\alpha }_g$ is its group expected value, $U_{gi}$ is a pot random effect, and ${\epsilon }_{gij}$ describes remaining variation among leaves and measurement error. Assume that all pot random effects are mutually independent, all remaining errors are mutually independent, and the two collections are independent of one another and of the randomization. These are explicit modelling assumptions, conditional on the assigned treatments; no normal distribution assumption is needed for the following variance calculation.

Two distinct leaf measurements in one pot share $U_{gi}$. Their covariance is ${\tau }^2$, their individual variance is ${\tau }^2+{\sigma }^2$, and their intraclass correlation coefficient isMeasurements from different pots have zero covariance and are independent under the stated statistical model. Statistical independence therefore concerns the whole response structure, not just the fact that the measured leaves are different objects.

An observational unit is the object or occasion supplying a recorded response. Several observational units can belong to one experimental unit; counting them as independent treatment replicates creates pseudoreplication.

An orthogonal block design has centered treatment-indicator vectors orthogonal to centered block-indicator vectors on the experimental units. With treatment replication $r_i$, block size $k_j$ and total $n$, this is equivalent to $n_{ij}=r_i{k}_j/n$. It permits additive block adjustment without changing treatment estimates.

A randomized complete block design groups similar experimental units into experimental blocks and places every treatment once in each experimental block, independently randomizing treatment allocation within experimental blocks. Blocking removes background between-block variation from within-block treatment comparisons. A balanced incomplete block design has $v$ treatments and $b$ experimental blocks of size $k<v$, with each treatment occurring in $r$ experimental blocks and every distinct treatment pair together in $\lambda$ experimental blocks. Counting treatment occurrences and co-occurrences gives $vr=bk$ and $r(k-1)=\lambda (v-1)$.

A Latin square of order $q$ places each of $q$ treatment symbols once in every row and every column of a $q\times q$ array. This controls two nuisance directions. A Graeco-Latin square superposes two mutually orthogonal Latin squares: each square is Latin, and each ordered pair of symbols from the two squares occurs exactly once. The two symbol factors can then be fitted together with row and column effects. Random permutations of row labels, column labels and treatment symbols provide a suitable randomized allocation without destroying these balances.

For the operator experiment, fit the additive normal linear modelHere $r_i,c_j$ account for the two fabric directions, and ${\tau }_o$ is the operator effect. Additivity, independent equal-variance errors and the normal assumption supply the exact F-test; there is only one observation per cell, so an unrestricted interaction model is not available.

In the analysis of variance for a Latin square, the three centered factor spaces each have dimension $4-1=3$. Together with the intercept the model has rank ten, leaving $16-10=6$ residual statistical degrees of freedom. The corrected total has $16-1=15$. The completed calculation isUnder the null hypothesis ${\tau }_1=\cdots ={\tau }_4=0$, the operator F-statistic isThe upper five-percent critical value for $F_{3,6}$ is $4.76$, so the operator effect is not significant at five percent in this model.

The decision is independent of the order of fitting rows, columns and operators. To prove the required orthogonality, let $u_i$ be any centered row coefficients and $w_o$ any centered operator coefficients. Their observation-space inner product is ${\sum }_{i,j}{u}_i{w}_{o(i,j)}={\sum }_i{u}_i{\sum }_o{w}_o=0$, since every operator occurs once in each row. The same calculation applies to columns and operators, and all row-column pairs occur once as well. Thus the three centered spaces are mutually orthogonal; their projections commute and sequential sums of squares equal adjusted sums of squares in every fitting order.

With machines included, the layout is a Graeco-Latin square: the machine symbols are Latin, and all sixteen operator-machine pairs occur exactly once. Fitin addition to the earlier constraints. The machine space contributes three new statistical degrees of freedom and is orthogonal to the previous factor spaces, so the operator sum of squares remains $18.25$. The residual sum of squares and statistical degrees of freedom becomeHenceThis exceeds $F_{3,3}(0.05)=9.28$ but not $F_{3,3}(0.01)=29.46$. Therefore the operator effect is now significant at five percent, but not at one percent. Adjustment for machines has removed substantial residual variation without altering the operator numerator. This illustrates why a balanced nuisance factor can change precision and significance even when it does not change the estimated treatment contrasts.

An orthogonal block design has treatment contrasts orthogonal to block contrasts after removing the grand mean. This is a statement about vectors on the experimental units, with the usual inner product; the two full spaces are not orthogonal because both contain the constant vector.

For a counting criterion, let $n_{ij}$ count experimental units receiving treatment $i$ in block $j$, let $r_i={\sum }_j{n}_{ij}$, let $k_j={\sum }_i{n}_{ij}$, and let $n={\sum }_i{r}_i$. The inner product of the centered indicators for treatment $i$ and block $j$ is $n_{ij}-r_i{k}_j/n$. ConsequentlyIn particular, equal-sized blocks must contain each treatment in the same proportion. Under an additive block-and-treatment model, adjustment for blocks then does not change the fitted treatment contrasts.

If the biological cells are initially interchangeable, randomly allocate them to five groups of ten for the days. Within each day, independently choose a uniform distribution on a finite set over assignments having two occurrences of each dose level to the ten experimental units. One implementation is a random permutation of a list containing two labels of each level; the duplicate labels give every admissible assignment the same number of underlying permutations.

Randomize the processing order within each day as well, while pairing each preparation with its immediate measurement. Randomize dose within day, not merely the names of the days. This restricted randomization preserves the planned balance while protecting treatment contrasts against systematic order effects. Conceal the dose labels from the assessor where practical.

Use a randomized complete block design, with day as block and each biological cell as an experimental unit. Each day should contain two biological cells at each of the five dose levels. Each level then has ten replicates overall and occurs equally often in every day: the resulting block design is an orthogonal block design.

This spreads any day-to-day changes in preparation, temperature or measurement across all levels instead of confounding dose with day. Treat the zero level as a control with otherwise comparable handling. Keep the treatment-to-measurement delay standardized because the response variable is a diffusion rate measured immediately after preparation.

The experimental unit is a volunteer on a particular afternoon, since that volunteer-session receives a program assignment. There are 36 such experimental units; a volunteer is a repeated block, rather than a unit that receives only one program throughout the experiment.

The observational unit is the individual completed sketch, equivalently the session's single recorded count of correctly represented features. The separate map features contribute to that response variable; they are not independently randomized replicates. Nor are repeated sessions on one volunteer independent subjects.

A completely randomized design uses $2m$ eligible animals, randomly selecting $m$ to receive $P$ and assigning the remainder to $Q$. Use comparable follow-up and assess the same response variable in both groups. Its advantage is simplicity and freedom from previous-treatment carryover effects; its disadvantage is that between-animal variation enters the residual and can make a treatment contrast imprecise.

A randomized complete block design with matched pairs first forms $m$ pairs using pre-treatment characteristics such as initial disease severity, age or breed. Independently choose which animal in each pair receives $P$, with its partner receiving $Q$. The experimental units are animals; pairs are blocks. The average within-pair difference estimates the treatment contrast, and positive within-pair similarity can reduce its variance. Its advantage is control of known heterogeneity; its disadvantage is the need for useful matching, with fewer residual statistical degrees of freedom and little gain if the matching variables are uninformative. Do not construct pairs using outcomes observed after assignment.

A two-period crossover design randomly assigns half the animals to sequence $PQ$ and half to $QP$. Each animal receives both treatments in separate periods, with a scientifically justified interval between them and the same outcome assessment after each period. Animal blocks remove persistent between-animal differences, while the two sequences balance treatment against period. Its advantage is potentially high precision from within-animal comparisons; its disadvantage is vulnerability to carryover effects, changing disease state and irreversible effects. It is suitable only when comparing the treatments in both periods remains meaningful and residual effects of the first treatment are adequately controlled. A two-period crossover design does not by itself disentangle arbitrary treatment-specific carryover effects.

First agree the scientific question and primary response variable. Ask the vet about the disease's course, the proposed mechanism and duration of each treatment, the eligible population, baseline severity, and what outcome and follow-up time would represent worthwhile improvement. Is the disease transmissible, is recovery reversible, and can treating one cow affect another's outcome? These answers determine whether a crossover design is credible, whether the experimental unit should be a cow or a whole herd, and whether individual randomization would leave interference between groups. Agree welfare and rescue arrangements with the vet when deciding which comparisons are feasible; the statistical plan cannot determine these from an unfamiliar disease name.

Second agree feasible allocation and adequate independent replication. Discuss numbers of available cows and herds, variation in the chosen outcome, a scientifically meaningful treatment difference, and the desired statistical power. Use these to plan sample size, rather than choosing a number solely from convenience. Discuss herd, lactation stage and initial severity as potential blocks in experimental design, then specify randomization, comparable management, concealed allocation and blinded outcome assessment where feasible. Repeated milk or health records from the same cow are observational units, not extra independent experimental units; pseudoreplication would give misleading standard errors. Availability of enough independent cows or herds, together with expected variation, governs the precision actually achievable.

Both factors are assigned at orchard level. Therefore the experimental units are the twelve orchards; the trees are observational units within them. The six combinations form a balanced factorial design, replicated twice. The orchard ANOVA stratum has $12-1=11$ statistical degrees of freedom. Spray uses $2-1=1$, pruning uses $3-1=2$, and their interaction term uses $(2-1)(3-1)=2$, leaving six for error.

Dividing each treatment sum of squares in ANOVA by its statistical degrees of freedom and using $1440/6=240$ as the denominator gives all missing entries:

The unrounded F-test statistics are $998/240=4.15833\dots$, $560/240=2.33333\dots$ and $202/240=0.841667\dots$. The within-orchard tree mean square in ANOVA, 180, is not the treatment error denominator: using it would confuse subsampling with independent replication. The tree ANOVA stratum has $12(30-1)=348$ statistical degrees of freedom; $1+11+348=360$ is the uncorrected total, and the corrected total is 359.

This produces a split-plot design: assign spray to whole orchards, with six sprayed and six unsprayed, then independently randomize ten trees to each pruning method inside every orchard. Orchards remain experimental units for spray; individual trees become experimental units for pruning. Pruning contrasts and the spray-by-pruning interaction term now lie in the within-block ANOVA stratum, while spray is tested between orchards.

The between-orchard ANOVA stratum has eleven statistical degrees of freedom, split into one for spray and ten for error. The within-orchard ANOVA stratum has 348, split into two for pruning, two for the interaction term and 344 for error. This pooling of within-orchard error is appropriate under the stated compound-symmetry covariance model; additional orchard-specific pruning variation would need its own variance component rather than this simplified error model.

The shared orchard effect cancels in a pruning difference within an orchard. Its variance is $2a/10$, so averaging across twelve orchards givesThe spray contrast still compares means of six orchards per group, each based on 30 trees, so its estimated variance remains $8/3$. For a difference of pruning differences between the two spray groups, each group's pruning difference has estimated variance $2\cdot 180/(10\cdot 6)=6$, and the resulting interaction contrast has estimated variance $12$, compared with $16$ in the original allocation.

Splitting pruning within orchards improves pruning and interaction precision without extra trees, and gives spray a less sparse error estimate; it does not reduce the spray contrast's variance. This option requires tree-level pruning to be practical without interference between neighboring trees. The numerical gains, like those in the other options, assume the current variance components remain applicable next year.