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Partition a regular factorial design by fixed signs of independent factorial contrasts. Products of those block-generating columns span the block effects. A treatment contrast that is constant on each block is therefore confounded with block differences. Select generators so that only scientifically dispensable treatment effects enter this space; randomize the assignment of blocks and the run order within each block.

A coded experimental variable rescales a physical setting ${\xi }_j$ around its center $c_j$, dividing by a chosen positive half-range $h_j$. The endpoints $c_j\pm h_j$ become $\pm 1$, giving dimensionless factorial design coordinates. The choice of scale affects the metric used for steepest ascent in response surface methodology.

For a linear regression model $Y_{bj}={\alpha }_b+f(x_{bj}{)}^T\beta +{ϵ}_{bj}$ with one unrestricted intercept per two-run experimental block, differencing the responses removes all experimental block effects. The parameter vector $\beta$ is identifiable precisely when the matrix whose rows are $f(x_{b1})-f(x_{b2})$ has full column rank. This criterion applies to arbitrary pairings, including nonregular factorial designs; requiring regular orthogonal confounding is a stronger constraint.

In a two-level factorial design, a factor subset defines a sign column. The coefficient of this column is its response contrast divided by the number of runs when the columns are orthogonal. A singleton describes a main effect and a pair describes a two-factor interaction. On the full cube, distinct columns have zero inner product: summing over any coordinate in their symmetric difference cancels the terms.

A factorial design includes every combination of specified factor levels. Balanced replication permits separate estimation of marginal effects and interaction terms. The factor allocation, not the number of subsamples, determines the appropriate error term for each effect.

A fractional factorial design uses a selected subset of the full factor-level combinations. In a regular two-level fraction, encode levels by signs and impose $k$ independent equations ${\prod }_{j\in G_i}{x}_j=s_i$. Independence of the generator incidence vectors over ${\mathbb{F}}_2$ leaves $2^{m-k}$ runs. Reduced run count creates aliasing in a fractional factorial design, which must be evaluated against the effects scientifically required.

Anxiety management techniques cover several different activities: recognising emotions and bodily sensations, providing psychoeducation, practising relaxation or controlled breathing, and teaching coping or problem solving routines. Their proposed functions also differ. A technique may make treatment understandable, help a young person engage with exposure, or be claimed to reduce anxiety as an active treatment ingredient. Evidence that a multicomponent CBT programme works does not establish that every included management technique is necessary or independently effective.

Historically, child CBT combined coping skills with practice approaching feared situations. Philip C. Kendall's 1994 trial randomised 47 nine- to thirteen-year-olds to a sixteen-session programme or waiting list and found clinical benefits, assessed across several informants and maintained at follow-up. This was important evidence that a structured psychological intervention could help childhood anxiety. Because skills and exposure were delivered together, and the comparator did not match active treatment, the trial did not isolate relaxation, coping statements or emotion identification as causal ingredients.^[ref]

The larger Child/Adolescent Anxiety Multimodal Study provides stronger evidence for the broader treatment package. John T. Walkup and colleagues randomised 488 seven- to seventeen-year-olds with separation, generalised or social anxiety to CBT, sertraline, their combination or pill placebo. At twelve weeks, 59.7% receiving CBT were rated much or very much improved, compared with 23.7% on placebo; combination treatment had an 80.7% response rate. These are global improvement rates, not percentages free of an anxiety diagnosis. The CBT arm included more than anxiety management skills, and pill placebo did not match every aspect of psychotherapy contact.^[ref]

Component research offers a more specific but less causally secure picture. Stephen P. H. Whiteside and colleagues analysed 75 studies containing 111 CBT conditions. Greater in-session exposure was associated with larger treatment effects, whereas relaxation was associated with smaller effects. The comparison was across differently constituted programmes rather than a random allocation of relaxation within the same exposure treatment. Differences in participants, treatment quality or the amount of exposure could therefore explain some of the association. It motivates dismantling trials; it does not establish that relaxation harms all anxious children.^[ref]

The conceptual issue is what learning the technique permits or prevents. Consider an adolescent who believes that an ordinary racing heart means an imminent catastrophe. Using a breathing exercise may reduce unpleasant arousal. If the adolescent concludes that catastrophe was avoided only because the exercise was performed perfectly, the original threat interpretation may remain intact. A different use of the same exercise, as an optional way to settle before continuing an agreed activity, need not imply that ordinary arousal is dangerous. Its function and the young person's explanation matter more than its label.

Similarly, identifying feelings can support communication and enable a child to describe what they predict. It is not evidence of improvement merely that they can correctly label a worksheet. Coping statements can function as predictions to test, or as reassurance repeated until the young person feels certain. Problem solving is appropriate when a realistic difficulty can be changed; repeatedly solving hypothetical worries can instead become another avoidance routine. These distinctions imply that engagement, immediate arousal and durable change in anxiety disorder should be measured separately.

Process evidence also cautions against using immediate calm as the sole success criterion. Peterman and colleagues found that most exposure-habituation indices did not predict subsequent outcome in their youth treatment sample. Although not a randomised component test, this challenges the assumption that a treatment exercise is ineffective whenever distress remains elevated. It supports assessing what a young person learns and subsequently does, alongside how they feel during the session.^[ref]

Developmental adaptation may still justify selected management elements. A younger child may need concrete examples of bodily sensations and a caregiver's help remembering a practice plan. An adolescent may prefer a collaborative explanation and private monitoring. Comprehension and participation should be checked directly rather than presumed from age. These potential benefits are reasons to study accessible delivery, not to infer that a long preparatory skills phase is essential for everyone. If preparation consumes most of the available sessions, it may reduce the opportunity to practise the behaviour that treatment is intended to change.

A decisive study would hold a competent exposure programme constant and randomise an additional clearly specified management module against contact-matched neutral material. Different modules should be distinguished, because a bundle of breathing, relaxation and cognitive work cannot identify the contribution of each. A factorial design could test an early psychoeducation or coping module separately from whether it is required during exposure. Fidelity assessment should record the actual use and meaning of skills, including whether they become perceived safety signals.

There are two relevant service questions. Adding a module while preserving exposure estimates its incremental benefit at an additional resource cost. Replacing exposure time with that module estimates its value under a fixed session budget. These comparisons should not be conflated. To justify removing a standard module as unnecessary, a sufficiently powered noninferiority design with a clinically justified margin would be more informative than a small superiority trial that simply fails to find a difference.

Outcomes should include masked diagnosis, everyday impairment, approach behaviour and longer-term return of fear, not only session distress. Early engagement, dropout, family burden and acceptability could reveal a helpful preparatory effect even without an independent symptom benefit. Repeated ratings of threat expectancy and arousal would test competing pathways, although mediator–outcome confounding remains possible. Prespecified developmental and diagnostic comparisons would indicate whether a module helps a particular subgroup without encouraging retrospective selection of favourable results.

By 2022, the strongest evidence supported CBT packages containing exposure, with substantially less certainty about the necessity or independent efficacy of generic anxiety management routines. Selected techniques can have a coherent role when they improve understanding or participation. Their use should be evaluated by whether they support effective learning and functioning, rather than by an assumption that successful treatment requires eliminating anxiety before a young person approaches a feared situation.

Anxiety disorders centrally involve cognition, but describing them solely as disorders of cognition is too strong unless the term is defined so broadly that it loses explanatory value. Threat appraisal, attention, interpretation and memory can contribute to excessive fear and avoidance. Bodily arousal, learning history, action and the environment also matter. A useful account specifies how these processes interact and asks whether changing a proposed cognitive process changes anxiety, rather than simply observing that anxious people report anxious thoughts.

David M. Clark's cognitive model of panic illustrates the explanatory gain. Ordinary sensations such as a racing heart can be interpreted as evidence of imminent catastrophe. Fear increases arousal, which provides further sensations for threatening interpretation. The account distinguishes the bodily input from its meaning and explains why similar sensations need not produce the same fear in different circumstances. It also predicts that precautions and avoidance can prevent disconfirmation. The 1986 paper supplied a mechanistic model, not by itself proof that every panic episode requires a consciously articulated catastrophic thought.^[ref]

The distinction between cognition and explicit verbal reasoning matters. A person may orient rapidly toward threat, experience an image or respond to a bodily sensation before they can describe a proposition. Absence of a reported sentence does not establish absence of information processing. Equally, a theory should not rescue itself from every negative finding by postulating an inaccessible belief. It must specify observable predictions and measures that can fail, including what would count as successful alteration of the proposed process.

Cross-sectional evidence is insufficient to establish direction. A threat interpretation could increase anxiety, anxiety could bias the interpretation, or a third factor could influence both. Questionnaires can also partly measure the same evaluative content on both sides of the association. Longitudinal prediction improves temporal ordering but leaves confounding possible. Experiments that manipulate interpretation or attention therefore offer a stronger test, especially when changes in the intended process are verified separately from changes in symptoms.

Andrew Mathews and Bundy Mackintosh reported five experiments inducing relatively threatening or benign interpretations of ambiguous material. Interpretative bias could be changed, but parallel effects on state anxiety depended on active processing of personally relevant meanings. This supports a causal contribution under specified conditions and shows that a changed task response need not automatically mean changed emotional experience. These experiments do not establish that an interpretation-training task is a complete treatment for a diagnosed anxiety disorder.^[ref]

Colin MacLeod and colleagues manipulated selective attention using a modified dot-probe procedure. The location of a subsequent probe was used to train attention in different directions relative to emotional material, followed by a standardised stress task. Differences in emotional vulnerability support a contribution from attention rather than association alone. Transfer from a laboratory induction to enduring clinical change, however, remains an additional question. Learning a task contingency, altered expectancies and the reliability of the process measure all require consideration.^[ref]

Clinical treatment comparisons provide complementary evidence. David M. Clark and colleagues compared cognitive therapy, applied relaxation and imipramine in panic disorder, with self-exposure homework shared across conditions. The findings supported cognitive therapy as a useful treatment. They do not make the comparison a pure test of thought change against an absence of learning or behavior: treatment packages differ in multiple ways, and a pharmacological treatment can also alter the sensations and experiences from which beliefs are formed.^[ref]

Safety behavior research further shows why a sharp cognition-versus-behavior division can mislead. Paul Salkovskis and colleagues found that changing precautions during exposure altered catastrophic beliefs and anxiety. The behavior may control which evidence is encountered and how success is explained. Conversely, a different explanation may make abandoning the behavior possible. These reciprocal effects favour a specified feedback system over treating observable action and mental representation as competing, self-contained causes.^[ref]

Learning accounts also need not exclude cognition. An inhibitory learning approach proposes that exposure establishes alternative expectations rather than necessarily erasing the original threat association. Context-dependent retrieval can explain return of fear after apparently successful practice. Michelle G. Craske and colleagues developed a translational framework around this distinction. It offers a way to connect expectation, experience and later retrieval, while its clinical implementation requires direct evaluation rather than assuming that a learning rationale proves a particular protocol optimal.^[ref]

The broader phrase 'anxiety disorders' also conceals heterogeneity. The feared consequence in social anxiety differs from the interpretation of bodily sensations in panic or persistent worry about many possible outcomes. A common information processing principle can coexist with disorder-relevant mechanisms. Actual danger and social adversity must be assessed: an expectation is not distorted simply because it concerns something distressing. Genetic, developmental and physiological influences can affect sensitivity to threat without fixing the meaning or outcome of every encounter.

Strong evidence for a particular cognitive mechanism would combine an experimental manipulation, a successful process check, subsequent change in fear and transfer to relevant everyday behavior. A factorial design could vary interpretation and a maintaining precaution separately, with matched contact and exposure opportunities. Repeated measurements should establish whether the cognitive change precedes the outcome. Treatment randomisation identifies the package effect, but mediation requires additional assumptions because the mediator itself has not necessarily been randomised.

Evidence against an exclusive account would include effective treatment without the predicted process change, or a precise null effect on anxiety after a successful, sufficiently strong manipulation of that process. Such a result might constrain the population or context in which the mechanism matters rather than rule out all cognitive contributions. Measurement sensitivity and alternative pathways must be considered without making the theory unfalsifiable.

The defensible conclusion is that cognition contributes materially to the persistence and modification of anxiety, with experimental evidence beyond introspective report. It is less defensible to claim that all anxiety disorders are caused only by consciously held false beliefs, or that the success of cognitive therapy establishes that exclusivity. Mechanistic precision and evidence about causal interaction are more informative than choosing between cognition, the body and behavior as if only one could matter.

A psychological treatment has a specific effect only relative to a clearly defined alternative explanation. Benefit beyond waiting is different from benefit beyond credible therapeutic contact, and both differ from evidence that a named technique works through its proposed mechanism. No single research design establishes all three. A persuasive programme combines controlled clinical comparisons with component and process experiments, while keeping patient-relevant outcomes central.

An uncontrolled before-and-after study cannot isolate a treatment effect. People may enter care when symptoms are unusually severe, creating regression toward their longer-term level; difficulties can improve naturally; expectations, concurrent care and repeated assessment can also change outcomes. A waiting-list randomised trial controls some time-related explanations but adds unequal expectations and contact. It can establish benefit from being offered the treatment package compared with waiting under those conditions, without identifying which ingredient produced the difference.

For specificity beyond nonspecific therapy effects, use a randomised comparison with a credible active intervention. Match time, attention, therapist competence and assessment opportunities as far as the question permits. Measure credibility and expected benefit rather than assuming equivalence from similar session counts. Keep relevant usual care available in both arms. Allocation concealment prevents recruitment decisions from anticipating the next assignment, while blinded independent outcome assessment reduces a different source of bias after allocation. Therapists and patients usually cannot be fully blinded to psychological procedures.

Daniel Freeman and colleagues' Feeling Safe trial illustrates this stronger package comparison. Patients with persistent persecutory delusions received the programme or befriending delivered by the same therapists, alongside usual care. At six months, the primary continuous conviction measure favoured Feeling Safe. This supports an effect beyond the particular befriending comparator, but does not establish that each module is necessary or that the whole benefit travelled through one nominated mediator.^[ref]

The comparator should be interpreted fairly. A weak or implausible control can exaggerate apparent specificity, while an active comparator may itself change the proposed mechanism. If befriending improves social confidence, it is not a biologically inert placebo. A null result may mean two useful treatments have similar effects, both are ineffective, or the study is too imprecise. Failure of a superiority test does not demonstrate equivalence; an equivalence or noninferiority question requires prespecified clinically justified margins and appropriate precision.

A dismantling trial varies a specified component while keeping the surrounding treatment adequate and similar. For example, compare the same exposure programme with and without a safety behavior intervention. This estimates a conditional contribution: absence of an additional benefit does not imply that the component is useless in every context, because another part may produce similar learning. A factorial design can independently vary an action and its explanatory rationale, estimating their effects and interaction when the study has adequate power.

The early panic safety behavior experiment provides both an example and a caution. Greater change after brief exposure with precautions reduced supports the combined manipulation. Yet behavioral instructions and the explanation of the exercise were not fully separated. The appropriate next test would vary those elements independently and check actual behavior and expectancy change. Simply renaming the conditions 'cognitive' and 'behavioral' would not remove the confounding.^[ref]

A mechanistic experiment can provide more direct leverage than a full treatment comparison. Colin MacLeod and colleagues trained attentional bias using a modified dot-probe task and tested later responses to stress. This asked whether experimentally changing information processing altered emotional vulnerability. It remains necessary to establish that the manipulation engaged the intended process rather than only a task-specific strategy, and that any effect transfers to the clinical phenomenon of interest. Laboratory emotional vulnerability is not itself diagnostic remission.^[ref]

Likewise, Daniel Freeman and colleagues used virtual social environments to compare exposure against threat testing with safety behavior reduction. Both groups encountered graded situations, making the content of learning more directly investigable than in a therapy-versus-waiting comparison. The combined manipulation and brief follow-up constrain the mechanism claim. A useful manipulation check, an independent behavioral outcome and later transfer assessment strengthen the design more than a treatment label does.^[ref]

Mediation analysis is informative but insufficient on its own. Randomising treatment identifies the total effect of assignment under the trial's assumptions; it does not automatically randomise the mediator. Symptom improvement could change reported beliefs, or an unmeasured process could influence both the belief score and the outcome. Measure the proposed mediator before the downstream outcome, assess competing pathways and perform sensitivity analyses. Replication using a different way to alter the same process can provide converging evidence; stronger identification may require experimental manipulation of that process itself.

Clinical trials also need suitable sampling, prespecified outcomes, adequate power, intention-to-treat analysis and transparent missing data handling. Outcomes should include functioning and possible deterioration, with follow-up long enough to distinguish transient reassurance from durable benefit. Treatment fidelity and competence must be assessed in both arms. Therapist allegiance, clustering of patients within therapists and differential dropout can affect interpretation. Statistical significance alone does not establish a meaningful improvement, especially when many outcomes or subgroup comparisons are explored.

Pragmatic implementation trials answer a complementary question: does the intervention add benefit in ordinary care, at acceptable cost and burden? Jaime Delgadillo and colleagues' therapist-cluster trial tested an automated feedback system linked to supervisory review within routine services. Its comparison isolates the added feedback arrangement more closely than an observational association between high-performing services and monitoring. It still tests a specified package of information and response, rather than an abstract effect of measurement divorced from clinical action.^[ref]

The strongest conclusion consequently states its level of specificity. A well-conducted active control trial can establish an incremental treatment-package effect. A dismantling or factorial trial can identify a component's contribution within a defined context. An experimental process manipulation, supported by temporally ordered measurements and converging clinical evidence, can constrain the mechanism. Keeping these claims separate prevents a successful therapy from being treated as proof of its entire theory, while preserving the practical importance of improvements patients actually experience.

TODO: the supplementary sheet is needed to identify the analysis actually conducted. A two-factor factorial design is described, but that alone does not distinguish an independent-groups two-way analysis of variance, a repeated-measures analysis of variance, a mixed design, or a mixed-effects model. The model call, error structure, participant allocation and output headings would establish which analysis was used. In particular, the prose does not establish that every participant experienced every condition.

The two independent variables are social-cue congruence, with congruent and incongruent levels, and cue-to-response delay, with short ($250$ ms) and long ($750$ ms) levels. The response variable is reproduction reaction time, measured in seconds. Thus the known treatment structure is a $2\times 2$ factorial design, potentially estimating two main effects and their interaction.

TODO: identify the allocation from the missing supplementary sheet or protocol. The eighty recruited participants do not establish whether either factor is within-subjects or between-subjects, whether all observations were retained, or how trials were summarized. The design cannot responsibly be called fully repeated-measures, fully independent-groups or mixed without that information.

TODO: an empirical Results section cannot be completed without the analysis and descriptive output. It must identify the actual factorial design, outcome scale and fitted model; summarize the four condition means with appropriately labeled standard deviations or standard errors; and report the congruence, delay and interaction tests with their actual F-test statistics, statistical degrees of freedom, p-values, effect sizes and relevant confidence intervals.

Interpret an interaction as evidence that the cue-congruence difference varies with delay, not merely as evidence that one separate test was significant and another was not. Any simple-effects analysis must identify its contrasts and multiple testing treatment. If the analysis used transformed reaction times, distinguish the model's scale from raw-second summaries. A nonsignificant result does not establish equality or absence of a theoretically meaningful effect. These are reporting requirements, not placeholders for invented results.

Code each factor level by $x_j\in \{-1,1\}$. A nonconstant factorial contrast indexed by a nonempty factor set $A$ has sign column $g_A(x)={\prod }_{j\in A}{x}_j$. Flipping any coordinate in $A$ reverses that sign and pairs the treatment combinations, so exactly $2^{m-1}$ have each sign. Allocating the two signs to two experimental blocks therefore divides the full factorial design into equal experimental blocks. The contrast is confounded with experimental blocks because its column is constant within each experimental block: changing its coefficient and compensating by the two experimental block intercepts leaves every fitted value unchanged. It has no information separate from experimental block differences. Randomize the allocation of the two groups to days and the run order within days.

Write $A,B,C$ for temperature, pressure and catalyst, respectively, with low levels and catalyst one coded minus. In the supplied allocation, $ABC=-1$ on day one and $ABC=1$ on day two. Thus the three-factor interaction $ABC$ is confounded with days. Every other nonconstant factorial column is orthogonal to the day contrast, because its product with $ABC$ is a nonconstant sign column on the full cube and consequently sums to zero.

If all interactions are negligible, the fitted model contains an intercept, one day contrast and the three main effects. The corrected total statistical degrees of freedom partition asThe three residual statistical degrees of freedom are the unused two-factor interaction columns $AB,AC,BC$, pooled as error under the stated negligible-interaction assumption. There is no independent pure-error replication of treatment combinations.

For four days with two runs each, all three main effects can be estimated. One regular allocation pairs each treatment combination with its complete opposite:The block-generating columns can be $AB$ and $AC$; their product $BC$ is also constant in experimental blocks. Thus $AB,AC,BC$ span the three experimental block contrasts, while $A,B,C$ and $ABC$ vary within experimental blocks. The main effects remain mutually orthogonal and separate from the experimental block effects; with an additive main-effect model there is one residual degree of freedom, represented by $ABC$.

For the further request about $AC$, the distinction between regular confounding and unrestricted pairing is important. A regular four-block allocation cannot retain all three main effects and $AC$. Its three confounded columns form a rank-two defining subgroup. To preserve main effects, these columns must lie in $\{AB,AC,BC,ABC\}$. If the subgroup includes $ABC$ and a two-factor column, their product is a main-effect column, which is forbidden. Hence the only permissible nonidentity subgroup is $\{AB,AC,BC\}$, and it necessarily confounds $AC$. This proves impossibility in the usual regular factorial-blocking framework, rather than relying on a count of available statistical degrees of freedom.

The literal request does not explicitly restrict arrangements to regular experimental blocks. If arbitrary pairings are permitted, a nonregular construction can estimate $A,B,C,AC$ together, assuming the other interactions are omitted from the model. An explicit allocation isEvery treatment combination occurs exactly once. Fit one unrestricted intercept per day and the four coefficients ${\beta }_A,{\beta }_B,{\beta }_C,{\beta }_{AC}$. By estimability from within-block differences, subtracting the second run from the first in each experimental block removes all day effects and yields the coefficient matrixThus all four coefficients are uniquely determined from the four day differences. In this broader design class the answer is yes, under the reduced four-effect model. The resulting fit is saturated: four experimental block intercepts plus four treatment coefficients use all eight observations, leaving no residual estimate of error variance. Replication or external error information would be needed for inference. This does not contradict the impossibility for regular orthogonal confounding, and it does not claim simultaneous unbiased estimation when arbitrary additional interactions are retained.

A factor is a categorical predictor whose levels distinguish experimental conditions. Two factors have a statistical interaction when the effect of changing one depends on the other's level. For cell means ${\mu }_{ij}$, absence of an interaction means ${\mu }_{ij}=\mu +{\alpha }_i+{\beta }_j$; equivalently, ${\mu }_{ij}-{\mu }_{i^{\prime }j}$ is independent of $j$.

Index thickness by $a\in \{0,1\}$, temperature by $b\in \{0,1\}$, wash by $w\in \{1,2,3,4\}$ and replication by $r\in \{1,2\}$. The full factorial design has the normal linear modelThe errors are independent with a common positive variance. Sum-to-zero constraints in each factor index, or the displayed treatment coding, identify the mean coefficients. This full model allows an arbitrary mean in each of the sixteen cells.

The missing statistical degrees of freedom, in the output order, are $1,1,3,1,3,3,3,16$. The first seven entries total fifteen; with the regression intercept there are sixteen mean coefficients among thirty-two observations, leaving sixteen residual statistical degrees of freedom. Balanced factorial orthogonality makes the term sums of squares in ANOVA independent of their ordering.

All terms involving wash have nonsignificant individual F-tests, and it is useful to test their removal jointly. The reduced model omits twelve mean coefficients. Its residual sum of squares is $57.09875$, compared with $32.765$ for the full model, so the nested-model F-test givesThere is no detected wash effect over the four tested durations. Removing its main effect and all its interaction terms respects the principle of marginality. Retaining the very large thickness-by-temperature interaction is essential: the thickness effect changes substantially with temperature.

With numeric indicators $a,b\in \{0,1\}$, treatment coding expresses the reduced fitted mean asThus the thin/low, thick/low, thin/high and thick/high fitted means are $4.225,5.6875,17.425,29.950$, respectively, at every wash level. Each is the sample mean of eight observations. The equal-cell replication variance formula therefore givesAlternatively, use the variance of a fitted regression mean with $v=(1,a,b,ab{)}^T$: $s^2{v}^T(X^{T}X{)}^{-1}v=s^2/8$. Individual coefficient standard errors cannot simply be added; their covariances enter the fitted-mean calculation.

Increasing temperature raises fitted lustre by $13.2$ for thin film and $24.2625$ for thick film. Increasing thickness raises it by $1.4625$ at low temperature and $12.525$ at high temperature. Their difference, $11.0625$, is the estimated interaction contrast; its standard error is $1.0098$, giving $t\simeq 10.956$ on twenty-eight statistical degrees of freedom. The interaction plot shows this strong departure from parallel mean lines, while the wash panel shows the much smaller variation across wash durations. Neither the nonsignificant wash test nor the plot proves that its true effect is exactly zero.

Let $Y_{ijkl}$ be the flight distance in millimetres for paper level $i$, launch-angle level $j$, design level $k$ and replicate $l$, where $i,j,k\in \{1,2\}$ and $l\in \{1,2\}$. The full factorial design is fitted by the normal linear modelThe assumptions are independent errors with a common variance and normal distribution, and the displayed factor-combination mean structure. The corner-point constraints areand $(PAD{)}_{ijk}=0$ whenever at least one index equals $1$. Thus the eight free mean coefficients are $\mu ,P_2,A_2,D_2,(PA{)}_{22},(PD{)}_{22},(AD{)}_{22},(PAD{)}_{222}$. These treatment coding coefficients are comparisons at the other factors' reference levels, rather than necessarily averaged main effects.

To test the three-factor interaction term, compare the full model with the model retaining all main effects and all two-factor interactions. The null hypothesis is $(PAD{)}_{222}=0$, against a nonzero value. Removing it increases the residual sum of squares by $21025$ and removes one parameter. With eight residual degrees of freedom, the nested-model F-test givesThere is no evidence that this three-factor interaction is needed. This does not establish that all two-factor interactions vanish: the paper-design interaction is substantial.

The stepAIC command performs stepwise selection by the Akaike information criterion. Its upper scope is the full factorial model and its lower scope is the intercept-only model. Starting from the full model, it compares admissible additions and deletions, preserving the hierarchy of interaction terms, and chooses changes that reduce the Akaike information criterion. With the supplied scope its default search permits both directions. For these Gaussian fits the displayed criterion, up to constants common to all models, is $16\log (\mathrm{RSS}/16)+2k$, where $k$ counts mean coefficients. The first deletion changes it from $226.72$ to $224.76$: the small increase in residual sum of squares is outweighed by removing a parameter. This is a greedy model selection procedure, not an exhaustive search or a sequence of fixed-level hypothesis tests. The command's arguments are described in the MASS documentation.

For the selected model, let $p=1_{\{i=2\}}$ and $d=1_{\{k=2\}}$. Thenindependently between flights. It has no angle term. The maximum-likelihood estimates of its mean coefficients are also obtained by ordinary least squares:For example, the four fitted means are just the four paper-design cell means, each averaging four flights over the angle levels. With $s^2=\mathrm{RSS}/12$, the variance-covariance matrix of the coefficient estimates is $s^2(X^{T}X{)}^{-1}$. Its diagonal gives the displayed standard errors; their ratios are $s/2,s/\sqrt{2},s/\sqrt{2},s$, with $s=892.6$ mm.

The final line of summary(model2.lm) is the joint nested-model F-test of $H_0:{\beta }_P={\beta }_D={\beta }_{PD}=0$, comparing this four-parameter model with a common mean. Its statistic iswith F-distribution $F_{3,12}$ under the fixed-model null and P-value $0.001057$. Thus the selected paper-design terms jointly improve the fit substantially. The coefficient of determination $0.7272$ means they account for about $72.7\%$ of the observed centred variation. These nominal inferential summaries do not adjust for the preceding model selection on the same data.

Using the unrounded fitted means givesin millimetres. Hence choose the high-performance design with the lighter paper; the fitted model leaves both launch angles tied, with expected distance about $5377$ mm. A preference for one angle is not supported by this selected model. The strong paper-design interaction reverses the design comparison: the simple design is better on heavy paper, whereas the high-performance design is better on light paper. Consequently a single design effect averaged over paper types would conceal the main result. There is little evidence here for an angle effect, and considerable flight-to-flight variability remains.

Before fitting, inspect raw-distance dot plots for all eight factor combinations, and interaction plots of cell means against design, with separate lines for paper and panels for angle. With only two replicates per cell, showing individual observations is more informative than elaborate box plots. These reveal reversals, spread and possible unusual flights. Afterwards inspect a residual-versus-fitted plot, a Q-Q plot of residuals, a scale-location plot, residuals against each factor and, if recorded, flight order, and Cook's distance for influential observations. Residual patterns by angle would question its deletion, while unequal spread or departures from the normal distribution would question the error assumptions rather than merely demand another mean term.

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.

A two-factor interaction means that changing one factor has a different effect at different levels of another. For a two-level factorial design, its sign column is $x_i{x}_j$, and four times its coefficient is the corresponding difference of differences. It can be confounded with other factorial contrasts in a fractional factorial design.