Sources and References

Primary textbooks — Huntington-Klein, N. (2022). The Effect: An Introduction to Research Design and Causality. CRC Press (free at theeffectbook.net); Hernán, M. A. & Robins, J. M. (2020). Causal Inference: What If. Chapman & Hall (free on Hernán’s Harvard website).

Supplementary texts — Angrist, J. D. & Pischke, J.-S. (2009). Mostly Harmless Econometrics. Princeton UP; Wooldridge, J. M. (2010). Econometric Analysis of Cross Section and Panel Data, 2nd ed. MIT Press.

Online resources — MIT OCW 14.771 (Development Economics); Andrew Goodman-Bacon (2021) on staggered DiD; Callaway & Sant’Anna (2021) on heterogeneous treatment effects in DiD.

Chapter 1: Causal Inference and Potential Outcomes

1.1 The Fundamental Problem of Causal Inference

The core challenge of microeconometrics is moving from observed data to causal claims. The potential outcomes framework (Rubin Causal Model) provides a rigorous language for causality.

The fundamental problem is that we observe only one potential outcome: \( Y_i = D_i Y_i(1) + (1-D_i)Y_i(0) \). We never observe the counterfactual for any individual.

Key estimands:

• ATE (Average Treatment Effect): \( \tau_{ATE} = E[Y_i(1) - Y_i(0)] \)
• ATT (Average Treatment Effect on the Treated): \( \tau_{ATT} = E[Y_i(1) - Y_i(0) \mid D_i = 1] \)
• ATC (Average Treatment Effect on Controls): \( \tau_{ATC} = E[Y_i(1) - Y_i(0) \mid D_i = 0] \)

The naive comparison \( E[Y_i \mid D_i = 1] - E[Y_i \mid D_i = 0] \) decomposes as:

Selection bias arises because treated and untreated units have different counterfactual outcomes even absent treatment.

1.2 Assignment Mechanisms

An assignment mechanism describes how treatment is allocated. Rubin’s taxonomy:

1. Randomized assignment: \( D_i \perp (Y_i(0), Y_i(1)) \). Randomization eliminates selection bias: \( E[Y_i(0)\mid D_i=1] = E[Y_i(0)\mid D_i=0] \), so the ATE and ATT coincide with the naive difference.

2. Unconfounded (ignorable) assignment: \( D_i \perp (Y_i(0), Y_i(1)) \mid \mathbf{X}_i \). Conditional on observables, treatment is as good as random. This is the identifying assumption for observational study methods like matching and regression.

3. Non-ignorable assignment: Unmeasured confounders exist. IV, DiD, RD, and synthetic control methods are needed.

1.3 SUTVA

The Stable Unit Treatment Value Assumption (SUTVA) has two parts:

1. No interference: Unit \( i \)’s potential outcomes do not depend on other units’ treatment status.
2. No hidden variations of treatment: There is only one version of treatment.

SUTVA is required for the potential outcomes notation to be well-defined. Violations (e.g., spillovers in network experiments) require extended models.

Chapter 2: Experiments and Regression in Experiments

2.1 Randomized Controlled Trials

In a randomized experiment, random assignment ensures \( E[Y_i(0)\mid D_i=1] = E[Y_i(0)\mid D_i=0] \), so:

This is the Neyman estimator. Its variance is:

where \( \sigma_j^2 = \text{Var}(Y_i(j)) \). Under the sharp null hypothesis \( H_0: Y_i(1) = Y_i(0) \) for all \( i \), randomization inference (Fisher’s exact p-value) is exact and requires no distributional assumptions.

2.2 Regression Adjustment in Experiments

Even in a randomized experiment, including pre-treatment covariates \( \mathbf{X}_i \) in a regression:

can improve precision by reducing residual variance, without affecting consistency of \( \hat{\tau} \). This is the Lin (2013) estimator with saturated interactions:

The coefficient \( \hat{\tau} \) estimates the ATE without any bias even if the regression model is misspecified.

Chapter 3: Unconfounded Assignment — Matching and Weighting

3.1 The Propensity Score

The propensity score is typically estimated by logit or probit. The overlap (common support) condition requires \( 0 < p(\mathbf{x}) < 1 \) for all \( \mathbf{x} \) — both treatment arms must be possible for every covariate value.

3.2 Matching Estimators

Matching pairs each treated unit with one or more control units having similar covariate values (or propensity scores) and computes the average outcome difference.

For nearest-neighbor matching (1-to-1, without replacement):

where \( \mathcal{M}(i) \) is the matched control unit. Matching bias arises from imperfect covariate balance; bias correction (Abadie-Imbens 2006) adds a regression adjustment to the match.

Propensity score matching matches on \( \hat{p}(\mathbf{X}_i) \) instead of the full covariate vector. Caliper matching discards treated units with no control within a specified propensity score distance.

3.3 Inverse Probability Weighting

IPW estimators reweight the sample to balance covariate distributions across treatment groups. The Horvitz-Thompson estimator for the ATE:

The augmented IPW (AIPW) or doubly-robust estimator combines a regression model \( \mu_j(\mathbf{x}) = E[Y_i(j)\mid\mathbf{X}_i = \mathbf{x}] \) with IPW weighting:

AIPW is doubly robust: consistent if either the propensity score model or the outcome model is correctly specified (but not necessarily both).

Chapter 4: Instrumental Variables for Causal Inference

4.1 Local Average Treatment Effect

In the IV framework with binary treatment and binary instrument, the Wald estimator identifies the Local Average Treatment Effect (LATE):

Under the potential outcomes IV assumptions (exclusion, relevance, monotonicity), this equals the ATE for compliers — units whose treatment status changes when the instrument changes (\( D_i(1) > D_i(0) \)).

The four compliance types under binary \( Z \) and binary \( D \):

Monotonicity rules out defiers. IV identifies the LATE for compliers only — the ATE for always-takers and never-takers is not identified.

4.2 Identification, Relevance, and Exclusion

Valid instruments must satisfy:

• Relevance: \( \text{Cov}(Z_i, D_i) \neq 0 \) (empirically testable via first-stage F-statistic).
• Exclusion restriction: \( Z_i \) affects \( Y_i \) only through \( D_i \) (non-testable assumption requiring substantive justification).
• Independence: \( Z_i \perp (Y_i(0), Y_i(1), D_i(0), D_i(1)) \) (approximately met by randomization or “as-good-as-random” assignment of \( Z_i \)).

Chapter 5: Difference-in-Differences

5.1 The Basic DiD Design

Difference-in-Differences (DiD) exploits panel data with two groups (treated and control) and two periods (pre and post intervention).

This can be estimated by OLS:

The coefficient \( \tau \) on the interaction term is the DiD estimate.

5.2 The Parallel Trends Assumption

DiD identifies \( \tau_{ATT} \) under the parallel trends assumption: absent treatment, the average outcome of the treated group would have evolved in parallel with the control group:

This assumption is untestable for the post-treatment period but can be assessed with pre-treatment placebo tests: testing whether the treated and control groups have parallel trends in periods before treatment.

5.3 Event Study Specification

An event study regression tests pre-trends and traces out treatment effects over time:

where \( T_i^* \) is the treatment timing, \( \alpha_i \) are unit fixed effects, \( \lambda_t \) are time fixed effects, and \( k = -1 \) is the omitted period (normalization). Coefficients for \( k < 0 \) are pre-treatment betas — if they are jointly zero, parallel pre-trends is supported.

5.4 Staggered DiD

When treatment is adopted at different times by different units (staggered adoption), the two-way fixed effects (TWFE) regression with a single binary treatment indicator \( D_{it} \):

estimates a weighted average of unit-time treatment effects, but the weights can be negative when treatment effects are heterogeneous across cohorts. This is the Goodman-Bacon (2021) decomposition problem. Modern estimators (Callaway-Sant’Anna, Sun-Abraham, de Chaisemartin-D’Haultfoeuille) construct valid ATT estimates by comparing each treated cohort only to clean control units not yet treated.

Chapter 6: Fixed Effects and Panel Data

6.1 Within-Unit Variation and Fixed Effects

As developed in ECON 323, the fixed effects estimator:

exploits within-unit variation while absorbing time-invariant unobservables. The ATT interpretation of \( \hat{\beta}_{FE} \) (in the DiD sense) relies on:

1. Strict exogeneity: \( E[\varepsilon_{it} \mid \mathbf{X}_{i1}, \ldots, \mathbf{X}_{iT}, a_i] = 0 \)
2. No anticipation and other timing assumptions

The workhorse causal panel model combines unit and time fixed effects (TWFE):

Unit FE control for any time-invariant confounders; time FE control for any unit-invariant shocks (e.g., aggregate business cycle, policy changes affecting all units simultaneously).

Chapter 7: Regression Discontinuity Designs

7.1 The Sharp RD Design

Regression Discontinuity (RD) exploits a cutoff rule: treatment is assigned based on whether a running variable \( X_i \) exceeds a threshold \( c \):

The identifying assumption is that potential outcomes \( E[Y_i(0) \mid X_i = x] \) and \( E[Y_i(1) \mid X_i = x] \) are continuous at the cutoff \( c \). Under this assumption, the discontinuous jump in observed outcomes at \( c \) identifies the treatment effect at the cutoff:

7.2 Estimation: Local Polynomial Regression

The standard estimator fits separate polynomial regressions on each side of the cutoff, evaluated at \( X_i = c \). Local linear regression (order 1):

where \( \hat{\alpha}_R \) and \( \hat{\alpha}_L \) are intercepts from local linear regressions within a bandwidth \( h \) on each side. The optimal bandwidth trades off bias (wider bandwidth picks up curvature in the regression function) and variance (narrower bandwidth uses fewer observations). The Imbens-Kalyanaraman (2012) and Calonico-Cattaneo-Titiunik (CCT 2014) data-driven bandwidth selectors are standard.

7.3 Validity Checks

1. Sorting test (McCrary density test): If units can precisely manipulate \( X_i \) to be just above \( c \), there will be a jump in the density of \( X_i \) at \( c \). Test for a discontinuity in the running variable density.
2. Covariate continuity: Pre-determined baseline covariates should be continuous at the cutoff if the design is valid.
3. Placebo cutoffs: Test for jumps in outcomes at arbitrary thresholds away from \( c \) — finding none supports the design.

7.4 The Fuzzy RD Design

When the cutoff only changes the probability of treatment (rather than determining it deterministically), the design is fuzzy. The Wald estimate for the fuzzy RD is:

This is a LATE for compliers at the cutoff, analogous to the IV LATE.

Chapter 8: Synthetic Control Method

8.1 Motivation

When the treated unit is a single region, country, or firm — and there is no natural comparison group satisfying parallel trends — the Synthetic Control Method (Abadie, Diamond & Hainmueller 2010) constructs a weighted combination of control units that best reproduces the treated unit’s pre-treatment trajectory.

8.2 Construction

Let unit 1 be treated at time \( T_0 \) and units \( 2, \ldots, J+1 \) be potential controls. Find weights \( \mathbf{w} = (w_2, \ldots, w_{J+1}) \) with \( w_j \geq 0 \) and \( \sum w_j = 1 \) solving:

where \( \mathbf{X}_j \) is a vector of pre-treatment predictors (lagged outcomes and covariates) for unit \( j \), and \( \|\cdot\|_V \) is a weighted norm with \( V \) chosen to minimize pre-treatment fit.

The synthetic control estimate is:

8.3 Inference via Placebo Tests

Classical asymptotics do not apply (usually \( J \) is small). Inference proceeds by applying the same synthetic control method to each control unit (as if it were treated at \( T_0 \)) and comparing the treatment unit’s post-treatment RMSPE to the distribution of placebo RMSPEs. A low p-value results when the treatment unit’s post-treatment gap is large relative to the placebo distribution.

Chapter 9: Implementation in R and Stata

9.1 Matching and IPW in R

library(MatchIt)
# Propensity score matching
m_out <- matchit(treat ~ age + educ + re74 + re75,
                 data = lalonde, method = "nearest",
                 distance = "logit", ratio = 1)
summary(m_out)  # balance statistics

library(WeightIt)
# IPW with logit propensity score
w_out <- weightit(treat ~ age + educ + re74 + re75,
                  data = lalonde, method = "ps", estimand = "ATT")
# Estimate ATT
library(marginaleffects)

9.2 Difference-in-Differences

library(did)
# Callaway-Sant'Anna estimator for staggered DiD
cs_out <- att_gt(yname = "lemp", gname = "first.treat",
                 idname = "countyreal", tname = "year",
                 data = mpdta, control_group = "nevertreated")
aggte(cs_out, type = "dynamic")  # event-study plot

9.3 Regression Discontinuity

library(rdrobust)
# Sharp RD with data-driven bandwidth
rdd_out <- rdrobust(y = outcome, x = running_var, c = cutoff)
summary(rdd_out)

# McCrary density test
library(rddensity)
rdd_density <- rddensity(X = running_var, c = cutoff)
summary(rdd_density)