Difference-in-Differences

Potential outcomes. Binary \(D\) gives two POs per unit-period: \(Y_{it}(0)\) and \(Y_{it}(1)\). Write

\[ Y_{it}(1) = Y_{it}(0) + \tau_i \]

with \(\tau_i\) unrestricted — no homogeneous-slope assumption. What the design recovers:

\[ \text{ATT} \;=\; E[\tau_i \mid G_i = 1] \]

— the mean effect on the treated. ATE would require restrictions on \(Y(1)\) too.

Next: Card & Krueger (1994) — DiD with two groups and two periods.

Policy: April 1992 — New Jersey raises minimum wage from $4.25 to $5.05. Pennsylvania does not.

Data:

• 410 fast-food restaurants in NJ and eastern PA — a minimum-wage-intensive industry, with wages tightly tied to the legal floor.
• Surveyed before (Feb–Mar 1992) and after (Nov–Dec 1992).

Outcome: average employment per restaurant.

Before-after — NJ alone, before vs. after:

\[ \bar Y_{\text{NJ, after}} \;-\; \bar Y_{\text{NJ, before}} \]

Confounded by time trends — economy-wide changes between Feb and Nov 1992.

DiD combines the two to cancel each one’s bias — formalized below.

The treatment indicator is the product:

\[ D_{it} = G_i \cdot T_t \]

— equals 1 only in the (treated, after) cell.

We observe outcome \(Y_{it}\) for every unit-period.

The observed outcome equals the PO under realized treatment:

\[ Y_{it} = D_{it} \cdot Y_{it}(1) + (1 - D_{it}) \cdot Y_{it}(0) \]

The fundamental problem: at any \((i, t)\), only one of \(\{Y_{it}(0), Y_{it}(1)\}\) is observed. The other is the counterfactual.

Substitute \(Y_{i1} = Y_{i1}(1)\) and \(Y_{i0} = Y_{i0}(0)\) for the treated group, then add and subtract \(E[Y_{i1}(0) \mid G=1]\):

\[ \begin{aligned} &= E[Y_{i1}(1) \mid G=1] - E[Y_{i0}(0) \mid G=1] \\ &= \underbrace{E[Y_{i1}(1) - Y_{i1}(0) \mid G=1]}_{\text{ATT}} + \underbrace{E[Y_{i1}(0) - Y_{i0}(0) \mid G=1]}_{\text{time trend (treated)}} \end{aligned} \]

Substitute observed = realized PO, then add and subtract \(E[Y_{i1}(0) \mid G=1]\):

\[ \begin{aligned} &= E[Y_{i1}(1) \mid G=1] - E[Y_{i1}(0) \mid G=0] \\ &= \underbrace{E[Y_{i1}(1) - Y_{i1}(0) \mid G=1]}_{\text{ATT}} + \underbrace{E[Y_{i1}(0) \mid G=1] - E[Y_{i1}(0) \mid G=0]}_{\text{selection bias}} \end{aligned} \]

The DiD idea: subtract the control’s before-after change from the treated’s. Let \(\bar Y_{g,t}\) denote the sample mean for group \(g\) in period \(t\):

\[ \hat\tau^{\text{DiD}} \;=\; \bigl(\bar Y_{1,1} - \bar Y_{1,0}\bigr) \;-\; \bigl(\bar Y_{0,1} - \bar Y_{0,0}\bigr) \]

The control’s change estimates the common \(Y(0)\)-trend — wiping out the time-trend bias in Naive 1.

Differencing across groups wipes out the group-level \(Y(0)\)-difference in Naive 2.

Both bias terms vanish — under an assumption we name next.

In words: absent treatment, both groups would experience the same average change in \(Y\).

A counterfactual statement:

• Left side is unobservable — the treated group’s no-treatment trend.
• Right side is observable — controls are never treated.
• PT equates an unobservable to an observable.

The dashed red line is the missing counterfactual. PT says it slopes the same as the control line. The vertical gap at \(t=1\) is the ATT.

Treatment effects can be heterogeneous. \(Y_{i1}(1) - Y_{i1}(0)\) can vary across units.

Only the average \(Y(0)\)-trends must match. It’s a statement about one potential outcome.

Compared to lect2a’s independence:

Like any causal inference, DiD breaks if SUTVA fails.

• \(E[Y_{i1}(1) \mid G_i = 1]\) — observed (treated, post).
• \(E[Y_{i1}(0) \mid G_i = 1]\) — counterfactual, reconstructed under PT.

Why ATT, not ATE? PT restricts \(Y(0)\) only. The control’s change estimates the treated group’s \(Y(0)\)-counterfactual — but tells us nothing about how controls would respond to treatment.

Add and subtract \(E[Y_{i1}(0) \mid G=1]\):

\[ \begin{aligned} =\;& \underbrace{E[Y_{i1}(1) - Y_{i1}(0) \mid G=1]}_{\text{ATT}} \\ &+ \underbrace{E[Y_{i1}(0) - Y_{i0}(0) \mid G=1] - E[Y_{i1}(0) - Y_{i0}(0) \mid G=0]}_{=\,0\text{ under PT}} \end{aligned} \]

Under parallel trends: \(\hat\tau^{\text{DiD}} \xrightarrow{p} \text{ATT}\). ✓

\[ \hat\tau^{\text{DiD}} \;=\; (+0.59) \;-\; (-2.16) \;=\; +2.75 \]

• Employment rose in NJ relative to PA after the wage hike.
• The design uses only two waves — a strict 2×2 DiD.

CK find \(\hat\tau > 0\). Two interpretations:

1. DiD failed: PT was violated, \(\hat\tau\) is biased upward, the “true” effect is negative or zero.

2. DiD worked: the competitive model is wrong about this labor market.

Subsequent literature has converged on (2). Why? — next.

• Wage-taking firms pay competitive wage \(w^*\).
• \(w_{\min} > w^*\) ⇒ employment falls to \(L_{\min}\).
• CK find the opposite — perfect competition is rejected by the data.

• Monopsony: marginal cost of labor exceeds supply ⇒ hires at \((L_m, w_m)\), below competitive.
• Min wage between \(w_m\) and \(w^*\) flattens MC ⇒ employment rises toward competitive.

Where the literature stands:

• Manning (2003): widespread evidence of monopsony in low-wage labor markets.
• Azar–Marinescu–Steinbaum (2022): local labor markets often have few competing employers — direct evidence of concentration.
• Post-CK minimum-wage research: moderate hikes show small/zero employment effects — consistent with frictional monopsony.

The CK lesson: a credible causal estimate can overturn a textbook prediction.

1. Compute the same number in standard software.

2. Get standard errors and confidence intervals.

3. Add covariates for precision or to relax PT.

4. Generalize naturally to many units and many periods.

The translation: replace the 2×2 cell structure with dummies and an interaction.

Reading off the coefficients:

• \(\alpha\): baseline — control group, pre-period.
• \(\beta\): group dummy — level shift for treated.
• \(\gamma\): time dummy — common shift after period.
• \(\tau\): interaction — extra shift for the (treated, after) cell. The DiD estimator.

\(\tau\) identifies the ATT under PT — proved on the Identification slide earlier.

Read off:

• Control change: \((\alpha + \gamma) - \alpha = \gamma\).
• Treated change: \((\alpha + \beta + \gamma + \tau) - (\alpha + \beta) = \gamma + \tau\).
• Difference of changes: \(\tau\).

\(\hat\tau^{\text{OLS}}\) equals the hand calculation by construction.

What we gain: SEs, CIs, and an extension framework — without changing the estimate.

Motivation 1 — Precision.

\[ Y_{it} \;=\; \alpha + \beta G_i + \gamma T_t + \tau(G_i \times T_t) + \boldsymbol\theta' W_i + U_{it} \]

If \(W_i\) predicts \(Y\), including it as a level reduces residual variance ⇒ tighter SE on \(\hat\tau\). Identification unchanged.

Motivation 2 — Conditional PT.

PT may fail unconditionally but hold within strata of \(W_i\). Needs a different spec — next slide.

PT may still hold given \(W_i\):

\[ E[Y_{i1}(0) - Y_{i0}(0) \mid G=1, W_i] \;=\; E[Y_{i1}(0) - Y_{i0}(0) \mid G=0, W_i] \]

\[ Y_{it} = \alpha + \beta G_i + \gamma T_t + \tau(G_i \times T_t) + \boldsymbol\theta' W_i + \boldsymbol\rho'(W_i \times T_t) + U_{it} \]

• \(\boldsymbol\theta' W_i\): \(W\)’s level effect.
• \(\boldsymbol\rho'(W_i \times T_t)\): change in \(W\)’s effect from pre to post.

\(W_i\) must be pre-treatment (lect4c, bad controls).

• \(\alpha_i\) — one intercept per restaurant. Absorbs state membership \(G_i\) and any time-invariant restaurant feature (location, owner, layout).
• The interaction \(G_i \times T_t\) is unchanged — same point estimate \(\hat\tau\).
• Residual variance shrinks \(\Rightarrow\) tighter SEs.

Identification is still group-level — PT compares treated and control \(Y(0)\)-trends. Unit FE is a regression-spec choice for precision, not a shift to unit-level identification.

• \(\lambda_t\) — one intercept per period (drop one for the dummy trap).
• \(D_{it} = G_i \cdot \mathbf{1}[t \geq t^*]\) — treatment indicator (1 only when \(i\) is treated and \(t\) is post).

Multiple pre-periods make PT testable — we can check whether the \(Y(0)\)-trend was parallel before treatment. Coming up.

• We cannot directly test PT in the treatment period.

• But with multiple pre-treatment periods, we can ask: did the groups move together before treatment?
• If yes, more plausible that they would have continued to move together absent treatment.

Caveat: parallel pre-trends are necessary but not sufficient for PT in the post-period. A coincidental shock at \(t^*\) could break post-period PT even if pre-trends are clean.

Notation: \(k = t - t^*\) is event time — periods relative to the treatment date.

• \(k = 0\): first treated period.
• \(k = -1\): last pre-treatment period (the reference — see below).
• \(k < -1\): earlier pre-periods (leads).
• \(k \geq 0\): post-periods (lags).

For a treated unit at event time \(k \neq -1\): \[Y_{it} = \alpha_i + \lambda_t + \beta_k + \varepsilon_{it}\]

So \(\beta_k\) is the treated-vs.-control gap at event time \(k\), relative to the gap at \(k = -1\).

• \(\beta_k\) for \(k < -1\): pre-period leads. Should be ≈ 0 if PT holds.
• \(\beta_k\) for \(k \geq 0\): post-period lags. Dynamic ATT at horizon \(k\).

Tested with a single \(F\)-statistic (or equivalent Wald test). Two failure modes:

1. Rejected — pre-trends are non-flat. PT is suspect.

2. Not rejected — consistent with PT, but does not prove PT in the post-period.

Always pair the test with a plot — a non-rejection can hide trended-but-noisy leads.

• (a) flat leads with CIs covering 0 — supportive of PT.
• (b) leads drift linearly toward 0; individual CIs all cover 0 — joint F-test likely doesn’t reject, yet the pattern is concerning. PT suspect.

Cluster at the group — the level above which observations are independent.

• lect6a TWFE: clustered at unit — serial correlation within unit.
• 6b DiD: cluster at group — serial + cross-sectional within group.

Few clusters (e.g., 2 states): wild bootstrap, or aggregate to group-period means.

Q1. If we include every event-time dummy (no reference), what goes wrong with OLS?

Q2. Which \(k\) should we drop by convention, and what do the remaining \(\beta_k\) then measure?

Slemrod (1995) — Tax Reform Act of 1986:

• Top marginal rate rose, effective Jan 1987.
• Anticipating, high-income earners pulled capital gains, bonuses, and other income into 1986 — locking in the lower rate.
• Pre-period outcomes reflected anticipation, not a clean no-treatment baseline.

• Diagnostic: re-estimate with \(k = -2\) as reference. A non-zero \(\hat\beta_{-1}\) then flags anticipation.
• Remedy: redate the treatment to the announcement date, not implementation.

• US states adopt a policy in different years.
• Firms get access to a new technology over a multi-year phase-in.
• Hospitals join a payment program on different dates.

The treatment indicator generalizes:

\[ D_{it} = \mathbf{1}[t \geq t_i^*] \]

— each unit has its own switch date \(t_i^*\). Untreated units have \(t_i^* = \infty\).

Natural approach: run TWFE with this \(D_{it}\) — \(y_{it} = \alpha_i + \lambda_t + \tau D_{it} + U_{it}\). But…

Goodman-Bacon (2021): TWFE’s \(\hat\tau\) is implicitly a weighted average of all 2×2 DiDs in the panel. With three units, the implicit comparisons include:

• A as control for B’s switch ✓ (clean)
• A as control for C’s switch ✓ (clean)
• C vs B around C’s switch ✗ — uses B (already treated) as a control

Callaway-Sant’Anna (2021): let \(\text{ATT}(g, t)\) = treatment effect on units treated at time \(g\), measured at time \(t\). Estimate each one as a clean 2×2 DiD using never-treated A as control.

Aggregate the cells (non-negative weights) → overall ATT, or average across cohorts at each event-time \(k = t - g\).

Variants on the same principle: Sun-Abraham (event study), dCdH (newly-treated vs not-yet-treated), BJS (impute counterfactual).