8. Experimental Design and Causal Inference

Introduction and Context

Business decisions are frequently expressed in causal language: a manager asks whether a price reduction will increase demand, whether leadership training will improve retention, or whether a new digital platform will raise productivity. Yet observational association is not causation. Firms that adopt advanced analytics may differ systematically from firms that do not; employees who volunteer for training may already be more motivated; and customers who receive a promotion may have been selected because they were likely to purchase. The central challenge of causal inference is therefore to estimate what would have happened under an alternative action, policy, or treatment.

Experimental design provides the strongest general framework for answering causal questions because it creates a comparison that approximates the counterfactual. When random assignment is feasible, treatment and control groups are expected to be comparable, on average, before the intervention. When randomization is infeasible, researchers rely on observational methods—including causal diagrams, matching, propensity scores, instrumental variables, regression discontinuity, difference-in-differences, and synthetic controls—to construct credible counterfactuals from available data.

For doctoral researchers and business analysts, causal inference is not simply a collection of statistical techniques. It is a disciplined process linking theory, research design, measurement, assumptions, estimation, sensitivity analysis, and substantive interpretation. A sophisticated model cannot rescue a poorly defined causal question or a design that violates its identifying assumptions.

Learning Objectives

By the end of this chapter, readers should be able to:

1. Distinguish causal effects from associations and define treatment, outcome, unit, and counterfactuals.

2. Design and evaluate randomized experiments, including factorial, cluster, and stepped-wedge designs.

3. Use potential-outcomes reasoning and directed acyclic graphs to clarify causal assumptions.

4. Select and critically assess matching, propensity-score, instrumental-variable, regression-discontinuity, difference-in-differences, and synthetic-control methods.

5. Diagnose threats such as confounding, spillovers, attrition, interference, anticipation, and manipulation.

6. Interpret causal estimates responsibly for managerial, organizational, and policy decisions.

7. Address ethical, governance, reproducibility, and emerging technology issues in causal analysis.

From Association to a Counterfactual Claim

Let unit i represent a customer, employee, store, firm, or market. Let D_i denote treatment status, where D_i=1 indicates exposure to an intervention and D_i=0 indicates non-exposure. Let Y_i(1) be the outcome that would occur for unit i under treatment and Y_i(0) the outcome that would occur without treatment. The individual causal effect is Y_i(1)-Y_i(0). Because the same unit cannot generally be observed simultaneously in both states, one of these outcomes is missing—the fundamental problem of causal inference.

A common estimand is the average treatment effect (ATE):

ATE = E[Y(1)-Y(0)].

For a population that actually received treatment, the average treatment effect on the treated (ATT) is E[Y(1)-Y(0)|D=1]. These quantities differ when treatment effects vary and treated units differ from untreated units. A policy maker may instead care about the average treatment effect on the untreated or a local effect for units near a threshold. Clear definition of the estimand prevents a frequent error: interpreting a result as universally applicable when it describes only a particular population, time, or treatment intensity.

The observed outcome can be represented as Y_i=D_iY_i(1)+(1-D_i)Y_i(0). Randomization makes treatment independent of potential outcomes in expectation. In observational data, however, treatment assignment may depend on measured or unmeasured characteristics. Confounding occurs when a common cause affects both treatment and outcome. Selection bias can also arise from conditioning on a collider—a variable influenced by two other variables—which may create a spurious association.

The stable unit treatment value assumption (SUTVA) combines two ideas: no interference between units and a well-defined treatment. If one customer’s treatment affects another customer’s outcome, or if “training” differs materially in content and delivery, a single potential outcome is not well defined. Business environments often violate SUTVA through peer effects, competition, network spillovers, and market equilibrium responses.

Designing Randomized Experiments

Randomized controlled trials (RCTs) assign units to treatment conditions using a probability mechanism. Randomization balances both observed and unobserved characteristics in expectation, allowing differences in mean outcomes to identify the causal effect. The simple estimator is the difference in average outcomes between treatment and control groups. Regression adjustment can improve precision, but it is not required for identification when randomization has been implemented correctly.

A credible experiment begins with a precise research question, a defined intervention, a primary outcome, a unit of randomization, and a target population. Power analysis should be conducted before data collection. It incorporates the minimum practically important effect, outcome variability, significance level, desired power, treatment allocation, clustering, and anticipated attrition. Statistical significance alone is not a substitute for practical importance: a very large sample may identify a trivial effect, whereas a valuable effect may be estimated imprecisely in a small sample.

The unit of assignment must match the mechanism of treatment and the risk of contamination. Individual assignment is efficient when participants do not influence one another. Cluster randomization assigns stores, branches, classrooms, teams, or geographic areas when treatment operates at group level or spillovers are likely. Because observations within a cluster are correlated, effective sample size is smaller than the raw number of observations. The intracluster correlation coefficient should therefore enter the power calculation and standard-error estimation.

A factorial design tests several interventions simultaneously. In a 2×2 design, for example, a firm can test two versions of a message and two levels of a discount, estimating both main effects and their interaction. Factorial designs are efficient but require adequate sample size and careful interpretation when interventions interact. Blocked or stratified randomization improves balance on important baseline characteristics, such as region or customer value. In a stepped-wedge design, clusters cross from control to treatment at different times; this can be useful when universal implementation is expected, but time trends and secular shocks must be modeled carefully.

Blinding, when feasible, reduces expectancy and measurement bias. In digital experiments, automated assignment and pre-specified analysis reduce researcher discretion. Intent-to-treat analysis estimates the effect of assignment, preserving the benefits of randomization even when participants do not comply. Per-protocol estimates the effect among those who followed the assigned treatment but may be confounded by compliance behavior. Treatment-on-the-treated estimates require additional assumptions and should not be casually substituted for the intent-to-treat effect.

Repeated testing, selective subgroup analysis, and stopping an experiment when a desired result appears can inflate false-positive risk. Pre-registration, a primary-outcome hierarchy, version-controlled code, and transparent reporting of deviations strengthen credibility. Ethical review is required when risks, privacy concerns, or vulnerable populations are involved. An experiment should not withhold an established effective service without a defensible rationale, and informed consent may be required even in organizational settings.

Causal Diagrams and Research Assumptions

A directed acyclic graph (DAG) represents variables as nodes and hypothesized causal relations as arrows. Suppose advertising (A) affects sales (Y), while seasonality (S) affects both advertising and sales. The backdoor path A←S→Y creates confounding. Conditioning on seasonality, either through design or analysis, can block this path. A DAG helps distinguish a confounder from a mediator. If advertising affects website visits, which then affect sales, website visits are a mediator. Controlling for it estimates a direct rather than total effect and may block part of the effect of interest.

A collider is a variable caused by two variables. If both advertising and customer demand influence whether a customer enters a sales funnel, conditioning on funnel entry can induce an association between advertising and demand. The practical lesson is not to control for every available variable. Covariate selection should follow a causal theory, temporal ordering, and the estimand.

The backdoor criterion states, informally, that a sufficient adjustment set contains variables that block all noncausal paths from treatment to outcome without conditioning on descendants of treatment. DAGs do not prove that a theory is correct; they make assumptions explicit and expose where evidence is weak. In doctoral research, diagrams should be developed before model estimation and revised when substantive knowledge or institutional processes indicate alternative pathways.

Observational Strategies for Constructing Comparisons

Matching and Propensity Scores

Matching attempts to compare treated units with untreated units that have similar pre-treatment characteristics. Exact matching is often impractical with many covariates. Propensity-score methods model the probability of treatment given observed covariates: e(X)=P(D=1|X). Under conditional exchangeability—no unmeasured confounding given X—and positivity—each relevant covariate profile has a nonzero probability of treatment and non-treatment—adjustment based on the propensity score can identify causal effects.

Common approaches include nearest-neighbor matching, caliper matching, stratification, inverse probability weighting, and doubly robust estimators. Doubly robust methods combine an outcome model with a treatment model and remain consistent if at least one is correctly specified under suitable conditions. The propensity score is a balancing device, not a magic correction for hidden bias. Variables should generally be measured before treatment; post-treatment variables can introduce bias.

After matching or weighting, analysts must examine covariate balance rather than merely report model fit. Standardized mean differences, variance comparisons, overlap plots, and effective sample size are useful diagnostics. Poor overlap indicates that the data do not support comparisons for some units. Trimming extreme weights may improve stability but changes the target population and must be disclosed. Matching can reduce sample size and precision, and unmeasured confounding remains a central threat.

Instrumental Variables

An instrumental variable Z changes treatment D but affects outcome Y only through D. The standard requirements are relevance, exclusion, and independence from unobserved determinants of the outcome. A lottery for access, an administrative assignment rule, or distance to a service provider may sometimes serve as an instrument, although each requires substantive justification.

Two-stage least squares first predicts treatment using the instrument and exogenous covariates, then relates the predicted treatment to the outcome. A weak instrument produces unstable estimates and magnifies bias; first-stage strength must therefore be assessed, although a conventional threshold is not a complete diagnostic. Under monotonicity and related assumptions, the instrumental-variable estimate is often interpreted as a local average treatment effect (LATE) for compliers—units whose treatment status is changed by the instrument—not necessarily the effect for all customers or employees.

The exclusion restriction is usually the most difficult assumption. For example, geographic distance may affect outcomes directly through travel burden, not only through treatment access. Instruments should be defended with institutional knowledge, falsification tests, alternative specifications, and sensitivity analysis rather than statistical convenience.

Regression Discontinuity Designs

A regression discontinuity (RD) design exploits a treatment rule based on whether a continuous assignment variable crosses a known cutoff. Firms may offer financing to applicants with a score above a threshold or provide assistance to branches below a performance boundary. Units immediately on either side of the cutoff are plausibly similar, so a discontinuity in the outcome estimates a local treatment effect.

The design requires continuity of potential outcomes at the threshold and no precise manipulation of the assignment variable. Researchers must choose a bandwidth and functional form; local polynomial methods and robust bias-corrected intervals are generally preferable to high-order global polynomials. Density tests, covariate continuity checks, placebo cutoffs, and graphical inspection can detect manipulation or specification problems. The estimate is local: it applies near the cutoff and may not generalize to units far away.

Fuzzy RD occurs when crossing the threshold changes treatment probability rather than treatment status deterministically. The discontinuity in treatment becomes an instrument for actual treatment, producing a local instrumental-variable effect. This is useful when eligibility rules are imperfectly implemented but complicates interpretation.

Difference-in-Differences

Difference-in-differences (DiD) compares changes over time in a treated group with changes in a comparison group:

DiD = (Y_T,post−Y_T,pre) − (Y_C,post−Y_C,pre).

The key identifying assumption is parallel trends: absent treatment, treated and comparison groups would have experienced the same average change. Pre-treatment trends cannot prove this assumption, but they can reveal serious implausibility. Analysts should inspect event-study graphs, test for anticipation, use appropriate fixed effects, and cluster standard errors at the level of treatment assignment.

With staggered adoption, conventional two-way fixed-effects estimators can be misleading when treatment effects vary across groups or time, because already-treated units may serve as controls for later-treated units. Modern group-time estimators and carefully specified event studies are preferable. DiD also faces threats from simultaneous policies, differential composition, spillovers, and changes in measurement.

Synthetic Controls

The synthetic-control method constructs a weighted combination of untreated units that reproduces the treated unit’s pre-intervention outcome trajectory and relevant predictors. The post-intervention gap between the treated unit and its synthetic counterpart estimates the effect. This is especially useful when one city, firm, country, or business unit receives a major intervention and many potential donor units are available.

The donor pool must be selected carefully. Units affected by the intervention, anticipation, or related shocks should be excluded. Pre-treatment fit is necessary but not sufficient: excellent fit can occur by chance, and poor fit undermines credibility. Placebo analyses apply the method to donor units to assess whether the observed post-treatment gap is unusual. Inference is often design-based or permutation-based rather than based on conventional large-sample formulas.

A Practical Workflow for Causal Analysis

A defensible analysis proceeds from the decision rather than from the dataset. First, state the intervention, population, time horizon, outcome, and estimand. Second, articulate a causal model using institutional knowledge and a DAG. Third, select the strongest feasible design, preferring randomization when ethical and operationally possible. Fourth, assess measurement quality, treatment fidelity, missingness, overlap, and timing. Fifth, pre-specify the primary analysis and plausible alternatives.

Estimation should be accompanied by diagnostics. These include balance and overlap for propensity methods; first-stage strength and exclusion arguments for instrumental variables; continuity and manipulation checks for RD; pre-trends and adoption timing for DiD; and pre-treatment fit and placebo tests for synthetic controls. Report effect sizes and uncertainty intervals, not only p-values. Where multiple outcomes or subgroups are examined, address multiplicity and distinguish confirmatory from exploratory findings.

Sensitivity analysis asks how strong an unmeasured confounder would need to be to overturn the conclusion. Researchers may use negative-control outcomes, Rosenbaum-type bounds, omitted-variable sensitivity analyses, or alternative comparison groups. Robustness is not demonstrated by presenting many models and selecting the most favorable result. It is demonstrated by explaining why reasonable analytic choices lead to similar substantive conclusions—or by honestly reporting where they do not.

Illustrative Case: Evaluating a Flexible-Work Policy

Background

A multinational professional-services firm introduces a flexible-work policy in 30 branches. Employees may work remotely up to three days per week. Senior leadership wants to know whether the policy improves retention without reducing client-service quality.

Situation and Problem

Branches volunteer for early adoption, creating a risk that adopters differ from non-adopters in leadership quality, labor-market conditions, and employee preferences. Retention is measured quarterly, while client satisfaction is reported monthly. Some employees change branches during the study, and managers begin discussing the policy before its formal implementation.

Analysis and Approach

If operationally possible, the strongest design would randomize eligible branches to immediate or delayed implementation. Because adoption has already begun, the research team first draws a DAG. Branch leadership, local labor-market conditions, employee autonomy, policy adoption, retention, and client satisfaction are included. Leadership and labor markets are pre-treatment confounders; employee morale may be both a cause of adoption and an outcome affected by the policy, so controlling for it after implementation could induce bias.

The team uses a staggered-adoption DiD with branch and quarter fixed effects, branch-specific pre-trends where justified, and standard errors clustered by branch. An event-study specification examines whether retention began changing before implementation, which would suggest anticipation or differential trends. Client satisfaction is analyzed separately because its timing and measurement differ. A propensity-weighted comparison is used as a robustness analysis, with balance and overlap reported.

Because employees may transfer between branches, the primary estimand is the effect of branch-level policy adoption on branch outcomes, not the effect on employees who personally use remote work. The team conducts an intent-to-treat-style analysis based on branch assignment to adoption timing and reports treatment uptake as a secondary measure. Missing survey responses are investigated rather than simply deleted; differential response rates could create apparent changes in satisfaction.

Outcome and Interpretation

Suppose the estimated retention improvement is positive but imprecise, while client satisfaction shows no meaningful decline. The correct conclusion is not that the policy definitively improves retention. A more defensible statement is that the evidence is consistent with a modest retention benefit and provides limited evidence of harm to client satisfaction, subject to parallel-trend and spillover assumptions. Management may choose a larger, randomized phased rollout, collect longer follow-up, and examine heterogeneous effects by role and caregiving responsibility.

Learning Points

The case illustrates that causal inference begins with estimand definition and institutional understanding. It also shows why adoption timing, anticipation, mobility, measurement, and heterogeneous treatment effects matter. A sophisticated estimator cannot eliminate bias caused by a poorly defined intervention or an invalid comparison group.

Limitations, Risks, and Common Errors

The most damaging error is treating statistical adjustment as equivalent to randomization. Observational methods can control only for measured and appropriately modeled confounding. Other frequent mistakes include conditioning on post-treatment variables, ignoring missing data mechanisms, using bad controls, extrapolating local estimates to a broad population, and reporting a statistically significant result without considering magnitude or cost.

Interference is especially important in business. A promotion may shift purchases between stores rather than increase total demand; training one team may change the performance of neighboring teams; and a pricing intervention may provoke competitor responses. Spillovers can invalidate standard treatment-control comparisons but may be substantively meaningful. Network experiments, cluster assignment, exposure mapping, or market-level designs may be more suitable.

Attrition can destroy comparability when treatment affects the likelihood of remaining observed. Differential measurement, changing definitions, seasonality, and algorithmic data collection can generate artificial effects. Machine-learning prediction models may improve nuisance-function estimation in doubly robust methods, but predictive accuracy does not establish causal validity. Flexible algorithms should be combined with cross-fitting, transparent feature construction, and a clearly stated causal design.

Ethical, Governance, and Professional Considerations

Causal research affects people’s access to services, employment opportunities, prices, and privacy. Researchers must establish lawful data use, informed consent where required, secure data handling, and proportionality between research risk and expected benefit. Automated experimentation should include safeguards against discriminatory allocation and harmful treatments. Protected characteristics should not be casually excluded from analysis; they may be essential for detecting unequal effects, although their use requires legal and ethical care.

Governance also concerns reproducibility. Analysis plans, treatment definitions, code, data dictionaries, version histories, and disclosure of deviations should be preserved. Confidential data may prevent public release, but researchers can provide synthetic data, code, or secure-access procedures. Decision makers should be told which assumptions are empirically testable, which depend on subject-matter judgment, and which remain uncertain.

Emerging Directions

Modern causal analytics increasingly combines experimental design with machine learning, real-time experimentation, and heterogeneous-treatment-effect estimation. Causal forests and related methods can explore which units benefit most, but subgroup discovery requires safeguards against overfitting and should be validated prospectively. Sequential experimentation and bandit systems optimize allocation while learning, yet they complicate conventional inference because treatment probabilities change over time.

Digital platforms enable rapid experimentation but also create concerns about consent, manipulation, interference, and platform-wide equilibrium effects. Transportability and generalizability are growing research priorities: an effect estimated in one firm, market, or period may not transfer when institutions, competitors, or user behavior change. The future of applied causal inference is therefore not merely more automated estimation; it is better integration of design, domain theory, transparent assumptions, and responsible deployment.

Best Practices for Doctoral and Professional Work

A high-quality causal study should:

• define the causal estimand before selecting a method;
• prefer randomization when feasible and ethically defensible;
• distinguish pre-treatment confounders, mediators, colliders, and instruments;
• justify the comparison group and target population;
• test overlap, balance, timing, trends, manipulation, and treatment fidelity;
• report uncertainty, practical significance, heterogeneity, and sensitivity analyses;
• separate confirmatory analyses from exploratory discovery;
• disclose missing data, attrition, interference, deviations, and model choices; and
• translate findings into decisions without overstating external validity.

Chapter Summary

Causal inference asks what would have happened under an alternative treatment or policy. Potential outcomes formalize this counterfactual question, while DAGs clarify causal pathways and adjustment choices. Randomized experiments identify causal effects through probabilistic assignment, but their validity depends on implementation, compliance, measurement, power, and ethical governance. When randomization is unavailable, matching and propensity scores rely on measured confounding and overlap; instrumental variables use external variation but often identify local effects; regression discontinuity exploits a threshold; difference-in-differences relies on credible parallel trends; and synthetic controls construct a weighted comparison for treated aggregate units. Each method is defined by assumptions, not merely by an estimation formula. Professional causal analysis therefore combines theory, design, diagnostics, sensitivity analysis, transparent reporting, and careful interpretation of scope.

Key Terms

Causal effect: The difference between outcomes under treatment and under a specified alternative for the same unit or population.

Counterfactual: The unobserved outcome that would have occurred under a treatment condition different from the one observed.

Potential outcome: An outcome defined for a unit under a particular treatment state.

Average treatment effect (ATE): The average difference between treated and untreated potential outcomes in a target population.

Average treatment effect on the treated (ATT): The average causal effect among units that received treatment.

SUTVA: The assumption of a well-defined treatment and no interference between units.

Confounder: A variable that causally influences both treatment and outcome and creates a noncausal association.

Collider: A variable caused by two other variables; conditioning on it can create bias.

Directed acyclic graph (DAG): A diagram of hypothesized causal relations without directed cycles.

Randomized controlled trial: An experiment in which treatment assignment is governed by a probability mechanism.

Intent-to-treat effect: The effect of being assigned to treatment, regardless of compliance.

Propensity score: The conditional probability of receiving treatment given observed covariates.

Positivity: The requirement that each relevant covariate profile has a positive probability of each treatment condition.

Instrumental variable: A variable that affects treatment but influences the outcome only through treatment, under identifying assumptions.

Local average treatment effect (LATE): The treatment effect for compliers whose treatment is changed by an instrument.

Regression discontinuity: A design using a treatment rule determined by crossing an assignment-variable cutoff.

Difference-in-differences: An estimator comparing before-after changes in treated and comparison groups.

Parallel trends: The DiD assumption that treated and comparison groups would have followed similar trends without treatment.

Synthetic control: A weighted combination of untreated units used to approximate a treated unit’s counterfactual trajectory.

Interference: A situation in which one unit’s treatment affects another unit’s outcome.

Review Questions

Short Answer Questions

1. Why is the individual causal effect generally unobservable?

2. Distinguish the ATE from the ATT.

3. What is the purpose of a DAG in causal research?

4. State the parallel-trends assumption in difference-in-differences.

5. Why can weak instruments produce unreliable instrumental-variable estimates?

Long Answer Questions

1. Explain how randomization, blocking, clustering, power analysis, and intent-to-treat analysis contribute to a credible experiment.

2. Compare matching and propensity-score methods with instrumental variables, emphasizing their assumptions and target populations.

3. Explain how regression discontinuity identifies a local causal effect and describe diagnostics for manipulation and model sensitivity.

4. Discuss the strengths and weaknesses of difference-in-differences and synthetic controls in business policy evaluation.

5. Develop a complete causal-analysis plan for evaluating a new employee development program.

Analytical / Application Questions

1. A retailer gives a loyalty discount to customers predicted to have low purchase frequency. Explain why a simple treated-versus-untreated comparison may be biased and propose a defensible design.

2. A firm implements a policy in different branches at different times. Describe how you would assess whether a staggered DiD design is credible and what threats you would investigate.

3. A government subsidy is available to firms with productivity scores above a fixed threshold. Explain how an RD design could estimate the subsidy’s effect and identify two reasons the estimate might fail to generalize.

22. Multiple Choice Questions with Answers

Question 1

Which quantity represents the average treatment effect on the treated?

A. E[Y(1)-Y(0)] for the entire population

B. E[Y(1)-Y(0)|D=1]

C. E[Y(1)|D=0]−E[Y(0)|D=1]

D. E[Y(1)+Y(0)|D=1]

Correct Answer: B. E[Y(1)-Y(0)|D=1]

Question 2

A manager controls for a variable that is caused by both advertising and customer demand. What problem may result?

A. Improved randomization

B. Removal of all confounding

C. Collider bias

D. Stronger positivity

Correct Answer: C. Collider bias

Question 3

What is the principal identifying assumption in a standard difference-in-differences design?

A. Treatment effects are identical for every unit

B. The outcome must be normally distributed

C. Treated and comparison groups would have followed parallel trends absent treatment

D. The treatment must be randomly assigned

Correct Answer: C. Treated and comparison groups would have followed parallel trends absent treatment

Question 4

What does intent-to-treat analysis estimate?

A. The effect among only fully compliant participants

B. The effect of assignment to treatment, regardless of compliance

C. The effect of treatment after controlling for all mediators

D. The effect only for participants near a cutoff

Correct Answer: B. The effect of assignment to treatment, regardless of compliance

Question 5

In an instrumental-variables design, which condition is especially difficult to defend substantively?

A. The outcome is measured numerically

B. The instrument has a first stage

C. The exclusion restriction

D. The sample contains untreated units

Correct Answer: C. The exclusion restriction

Question 6

A regression-discontinuity estimate is usually best interpreted as:

A. A universal treatment effect for all populations

B. A local effect near the assignment cutoff

C. A purely descriptive correlation

D. An effect identified only through random assignment

Correct Answer: B. A local effect near the assignment cutoff

Question 7

Which diagnostic is most directly relevant after propensity-score matching?

A. Covariate balance and overlap

B. Whether the outcome has a high mean

C. Whether all observations have identical treatment effects

D. Whether the treatment coefficient is positive

Correct Answer: A. Covariate balance and overlap

Question 8

Why can conventional two-way fixed-effects DiD estimators be problematic with staggered adoption?

A. They cannot include time indicators

B. They may use already-treated units as controls when effects vary over time

C. They require a continuous treatment variable

D. They eliminate all pre-treatment information

Correct Answer: B. They may use already-treated units as controls when effects vary over time

Question 9

What is the main purpose of a synthetic control?

A. To replace missing individual-level outcomes

B. To construct a weighted untreated comparison for a treated aggregate unit

C. To guarantee random assignment

D. To estimate only individual treatment effects

Correct Answer: B. To construct a weighted untreated comparison for a treated aggregate unit

Question 10

A digital experiment finds a statistically significant effect that is extremely small and costly to implement. What is the most appropriate interpretation?

A. Statistical significance proves the policy is worthwhile

B. The effect should be ignored because it is statistically significant

C. Practical importance and implementation costs must be assessed alongside uncertainty

D. The result automatically generalizes to every organization

Correct Answer: C. Practical importance and implementation costs must be assessed alongside uncertainty