Purpose

This workflow helps business PhD and DBA researchers connect a causal question to an explicit identification strategy. Four independent synthetic studies illustrate digital adoption, a common-date rollout, encouragement to adopt, and a grant cutoff. They are not alternative estimators applied to one dataset, and their effect estimates should not be compared as a horse race.

Public preview: Outputs and guidance only. The paid version includes all editable R Markdown, analysis code, reusable functions, synthetic data, diagnostics, and exported results.

You will define estimands, audit assignment and overlap, estimate effects with design-appropriate uncertainty, examine falsification and sensitivity results, and produce reporting language. Prerequisites are linear regression, basic R, and a substantive understanding of treatment timing and confounding. This is a teaching workflow; a significant coefficient does not establish identification.

Settings and data

For real data, set use_synthetic to FALSE and supply all four input files with the schemas in the data dictionary. These are four separate worked designs; keep only the relevant sections in a study-specific copy. Recenter a real RD score so that the cutoff is zero. A missing-data strategy must be chosen before running: this workflow deliberately stops on incomplete required inputs. It does not impute or silently delete cases.

Input audit: unique firm keys, complete required values, and treatment coding are checked before estimation.
design rows firms missing
observational 900 900 0
did 1800 180 0
iv 1000 1000 0
rd 1400 1400 0

Choose the estimand before the model

Design Target in this example Identification requirement
Weighting ATE in the sampled firm population No unmeasured confounding given pretreatment size, age, and sector; overlap; consistency
Difference-in-differences Average post-adoption ATT Parallel untreated trends; no anticipation; no spillovers; common adoption date
Instrumental variables LATE among encouragement compliers Relevant randomized encouragement; exclusion; monotonicity; no interference
Sharp RD Local effect at the grant cutoff Continuity of potential outcomes; no precise manipulation; deterministic assignment

Before adjustment, sketch a causal diagram. In the weighting example, size, age, and sector precede both adoption and productivity. Do not adjust for a mediator such as post-adoption training or a collider such as selection into a performance award. Sampling weights, propensity weights, and precision weights answer different questions.

Observational adoption and weighting

Overlap and balance

Standardized mean differences; both columns use the same unweighted pooled SD.
variable before after
size_z 0.597 -0.004
age -0.147 0.008
sector 0.104 0.008
Effective sample sizes describe weight concentration; they are not degrees of freedom.
adopt n effective_n max_weight
0 550 508.469 5.265
1 350 295.283 9.089

The largest absolute weighted SMD is 0.008. Values around 0.10 are a review convention, not a proof of exchangeability. Check distributional overlap and nonlinear terms, not only means. The largest weight is 9.09. Extreme weights signal limited support; trimming changes the target population and should be prespecified and reported. No automatic trimming is applied here.

ATE with a refitted bootstrap

The Hájek estimate normalizes weights within adoption groups. The bootstrap resamples independent firms and refits the propensity model every time, capturing estimated-weight uncertainty. If firms are clustered in markets or firms repeat, resample the independent assignment clusters instead. Bootstrap intervals do not repair confounding or poor overlap.

ATE with a percentile bootstrap interval.
estimate std_error lower upper replicates
4.091 0.36 3.367 4.798 1999

Results text: In 900 firms, the weighted productivity difference was 4.09 points, 95% bootstrap CI [3.37, 4.80], based on 1999 resamples. Interpretation as the ATE requires adequate overlap, the stated measured-confounding model, and no unmeasured confounding. Check interval stability across seeds or additional replicates before final reporting.

Common-adoption difference-in-differences

Firm fixed effects absorb stable differences; year effects absorb common shocks. Treatment is assigned at the firm level, so both the aggregate model and event-study intervals cluster by firm. This example has one treatment date and never-treated controls. Do not reuse this two-way fixed-effects event study unchanged for staggered adoption with heterogeneous effects.

model term estimate std_error p lower upper
Average post-adoption ATT treated:post 3.391 0.274 p < .001 2.851 3.932
test F p df1 df2
Joint pre-adoption coefficients 1.974 p = .100 4 179

Results text: The estimated average post-adoption ATT was b = 3.39, 95% CI [2.85, 3.93], p < .001. The event-study preperiod test returned p = .100. A nonsignificant pretrend test does not prove parallel trends: consider power, economic plausibility, concurrent policies, and changing sample composition. The intervals are pointwise, not simultaneous. The design uses 180 firm clusters; few-cluster studies need different inference, such as an appropriate wild-cluster procedure or randomization inference.

At the .05 level, the joint preperiod test does not reject zero preperiod contrasts. This is an absence of detected joint differences, not affirmative evidence that untreated trends would remain parallel.

Instrumental variables: randomized encouragement

Encouragement increases adoption, but some firms adopt regardless and others never adopt. The synthetic instrument is randomized and affects productivity only through adoption; unobserved uptake propensity also predicts the outcome. These assumptions are known because this is a simulation. A real encouragement may directly change behavior and violate exclusion. LATE applies to compliers, not necessarily all firms.

First-stage encouragement contrast in adoption probability (linear probability model).
model term estimate std_error p lower upper
OLS association adopt 6.622 0.331 p < .001 5.973 7.271
2SLS LATE fit_adopt 4.981 0.900 p < .001 3.214 6.747
model term estimate std_error p lower upper
First stage encouraged 0.364 0.029 p < .001 0.307 0.421
model term estimate std_error p lower upper
Reduced form / ITT encouraged 1.813 0.379 p < .001 1.069 2.557

The single-instrument heteroskedasticity-robust first-stage Wald statistic is 159.45. A cutoff such as 10 is not a universal assurance of strong identification. Two-stage least squares standard errors come from the IV estimator, not an ordinary regression on fitted treatment. Here the 2SLS estimate is b = 4.98, 95% CI [3.21, 6.75], p < .001. Compare this with the OLS association to illustrate endogeneity, not to prove the IV assumptions.

Weak-instrument-aware sensitivity

For each hypothesized effect, the Anderson–Rubin-style test regresses outcome minus the hypothesized effect times adoption on encouragement and the exogenous covariate. The heteroskedasticity-robust test is asymptotic; inversion can yield wide, disconnected, or unbounded sets. This finite grid is a diagnostic, not an exact endpoint calculation.

Accepted grid values range from 3.25 to 6.50. Acceptance does not reach the tested grid boundaries. The complete accepted set is available in the exported grid; a range alone can hide disconnected regions. With one excluded instrument the model is exactly identified, so there is no overidentification test. No statistical diagnostic verifies exclusion or monotonicity.

Sharp regression discontinuity

Firms with a score of zero or higher receive a grant. The effect pertains to firms near the threshold. Use local linear fits and robust bias-corrected inference from rdrobust, with a data-selected bandwidth. Do not extrapolate the local effect to all applicants or replace the local model with a high-order global polynomial.

Sensitivity varies both estimation and bias-correction bandwidths; it is not model selection by significance.
model estimate std_error p lower upper bandwidth_left bandwidth_right local_left local_right
Main bandwidth: robust bias-corrected 7.217 1.186 p < .001 4.892 9.543 20.783 20.783 284 266
model estimate std_error p lower upper bandwidth_left bandwidth_right local_left local_right
Bandwidth x 0.75 7.629 1.374 p < .001 4.936 10.322 15.587 15.587 213 193
Bandwidth x 1 7.217 1.186 p < .001 4.892 9.543 20.783 20.783 284 266
Bandwidth x 1.25 6.848 1.081 p < .001 4.729 8.966 25.978 25.978 356 341
model estimate std_error p lower upper bandwidth_left bandwidth_right local_left local_right
Pretreatment outcome continuity check 0.237 1.185 p = .841 -2.086 2.56 15.976 15.976 220 201

Results text: At the eligibility cutoff, the estimated bias-corrected productivity discontinuity was b = 7.22, 95% CI [4.89, 9.54], p < .001, using local linear regressions with triangular weights and 284 observations to the left and 266 to the right. The interval uses robust bias correction. A pretreatment outcome check is only one falsification exercise; it does not establish continuity of all potential outcomes.

For real applications, investigate score construction, discretion, heaping, other rules at the cutoff, and missing applicants. Add an appropriate density/manipulation test (for example rddensity) and design-specific placebo cutoffs; they are not implemented here. A donut exclusion changes the local support and needs substantive justification. Fuzzy assignment requires a fuzzy RD estimator, not this sharp design.

Reporting checklist

  • Define the treatment, comparison, time zero, outcome window, unit, and estimand.
  • Explain why the assignment mechanism supports identification; record a causal diagram and pretreatment covariates.
  • Report inclusion/exclusion, missingness, sample and cluster counts, weight diagnostics, and bandwidths where applicable.
  • Identify the exact estimator and covariance/interval procedure; report effect sizes and uncertainty in outcome units.
  • Report falsification results and prespecified sensitivity checks, including unfavorable findings.
  • Separate statistical uncertainty from threats to identification and transportability.
  • State package versions, seeds, and deviations from the analysis plan.

When this workflow is not enough

Staggered adoption, heterogeneous effects with changing treatment cohorts, anticipation, treatment reversal, spillovers, time-varying confounding, weak instruments, few clusters, fuzzy or discrete-score RD, and endogenous sample selection require extensions. Do not interpret a firm fixed-effect regression as causal merely because fixed effects are included. For clustered assignment, the number of independent treatment units—not the number of firm-year rows—drives design strength. Power planning should simulate the intended assignment process and estimator.

References and next steps

All examples are synthetic and do not reproduce proprietary business databases or dissertation datasets.