The identification toolkit so far:

• Chapter 3: Control for observed confounders (regression, matching)
• Chapter 4: Use instruments when confounders are unobserved
• Chapter 5: Exploit time/cohort dimension when confounders are unobserved but fixed

Conditional independence:

E(y_0it | A_i, X_it, t, d_it) = E(y_0it | A_i, X_it, t)

Union status is as good as randomly assigned conditional on unobserved ability A_i, observed covariates X_it, and time.

Why does this work algebraically?

By the regression anatomy formula (3.1.3), estimating with a full set of person dummies is the same as regressing on the residuals from a regression on those dummies. The residuals from regressing on person dummies are exactly deviations from person means.

Random effects assumes α_i is uncorrelated with the regressors. Then α_i becomes part of the residual (no OVB from ignoring it), but residuals for a given person are correlated across periods.

The authors prefer: OLS with fixed effects + robust standard errors, rather than GLS under random effects. GLS requires stronger assumptions (linear CEF, homoskedasticity) and efficiency gains are typically modest.

FE estimates are notoriously susceptible to attenuation bias:

• Economic variables like union status tend to be persistent (a union member this year is likely a union member next year)
• Measurement error often changes year-to-year (union status may be misreported this year but not next)
• → While few workers are misclassified in any single year, observed year-to-year changes in union status may be mostly noise
• → More measurement error in Δd_it than in d_it → FE estimates biased toward zero

Twins and Returns to Schooling:

Ashenfelter & Krueger (1994) and Ashenfelter & Rouse (1998) estimate returns to schooling using twins, controlling for family fixed effects (common family/genetic background).

Surprising result: Within-family estimates are larger than OLS!

Bound & Solon (1999) critique:

• Even twins have small differences: first-borns typically have higher birth weight and higher IQ
• While within-twin differences are small, so is the difference in their schooling
• → A small amount of unobserved ability differences could cause substantial bias

Natural experiment:

• April 1, 1992: New Jersey raised state minimum from $4.25 to $5.05
• Pennsylvania: Stayed at $4.25 (federal minimum)
• Data: Employment at fast food restaurants (Burger King, Wendy's, etc.) in NJ and eastern PA
• Timing: February 1992 (before) and November 1992 (after)

Control state (PA):

E[y|PA, Nov] − E[y|PA, Feb] = λ_Nov − λ_Feb

Treatment state (NJ):

E[y|NJ, Nov] − E[y|NJ, Feb] = λ_Nov − λ_Feb + δ

Difference-in-differences:

[E[y|NJ, Nov] − E[y|NJ, Feb]] − [E[y|PA, Nov] − E[y|PA, Feb]] = δ

Interpretation:

• PA employment fell by 2.16 workers per store
• NJ employment rose by 0.59 workers per store
• DD = +2.76 — opposite of standard prediction!
• Higher minimum wage did not reduce employment; if anything, it slightly increased it

Employment
    │
    │                    ●───────● Treatment (observed)
    │                   ╱         
    │                  ╱  ← Treatment effect (δ)
    │                 ╱           
    │                ●─ ─ ─ ─ ─ ●  Counterfactual
    │               ╱               (parallel to control)
    │              ╱
    │  ●─────────●  Control (observed)
    │
    └────────────────────────────── Time
              Before      After

Key insight: We never observe the counterfactual.
The parallel trends assumption lets us use
the control group's change as a proxy.
                

Card & Krueger (2000) Follow-up:

Administrative payroll data for restaurants in NJ and PA for multiple years reveal:

• Feb-Nov 1992: Slight PA decline, little NJ change (consistent with original survey)
• But: Substantial year-to-year variation in other periods
• Employment swings often differ substantially between states
• PA employment fell relative to NJ over 1992-1995, mostly before the 1996 federal minimum increase

Concern: PA may not provide a good measure of counterfactual NJ employment.

Better Example: Pischke (2007) — German School Term Length

• Until 1960s: German states (except Bavaria) started school in Spring
• 1966-67: Non-Bavarian states switched to Fall start
• Transition required two short school years (24 weeks instead of 37)
• Outcome: Grade repetition rates for 2nd graders

Results:

• Bavaria (control): Flat repetition rates ~2.5% from 1966 onwards
• Treatment states: Higher baseline (~4-4.5%), jump by ~1 percentage point for affected cohorts, then return to baseline
• → Strong visual evidence of parallel trends + transitory treatment effect

Example: Card (1992) — Federal Minimum Wage

In 1990, federal minimum increased from $3.35 to $3.80. Impact varies by state (irrelevant in high-wage Connecticut, big deal in low-wage Mississippi).

where fa_s = baseline fraction of teens earning below $3.80 in state s (treatment intensity).

Example: Autor (2003) — Employment Protection & Temp Workers

State court rulings allowing "unjust dismissal" lawsuits → Do firms use more temp workers?

Estimated leads and lags pattern:

• 2 years before, 1 year before: No effect (leads ≈ 0) ✓
• Year of adoption: Small positive effect
• 1-3 years after: Sharply increasing effects
• 4+ years after: Effects flatten at permanently higher level

This pattern is consistent with a causal interpretation: no anticipation, gradual adjustment.

Example: Besley & Burgess (2004) — Labor Regulation in India

Interpretation: Without trends, labor regulation appears to reduce output. With state trends, the effect disappears → regulation increased in states where output was already declining.

Example: Welfare benefits and labor supply

If generous welfare states attract poor people with weak labor force attachment (program-induced migration), DD makes generous welfare look worse for labor supply than it really is.

Fix: Use state of birth or previous residence (unchanged by treatment but correlated with current location). This can be implemented as an IV strategy.

Example: Yelowitz (1995) — Medicaid Expansion

Medicaid eligibility was once tied to AFDC (cash welfare). In the 1980s, some states extended coverage to children in families ineligible for AFDC.

Treatment varies by state, time, and child's age. DDD compares across all three dimensions, providing more convincing control than standard DD.

Example: Training Program Evaluation

People in government training programs have often suffered a recent setback (job loss). Many programs explicitly target such people.

Ashenfelter (1978), Ashenfelter & Card (1985): Training participants exhibit a pre-program earnings dip.

Past earnings is a time-varying confounder that cannot be subsumed in a time-invariant α_i.

Nickell (1981) Problem:

Δy_it−1 = y_it−1 − y_it−2 contains ε_it−1

Δε_it = ε_it − ε_it−1 also contains ε_it−1

→ Regressor correlated with error! OLS is inconsistent.

1. Check robustness: Estimate both FE and LDV models. If they give similar results, you can be more confident.
2. Interpret as bounds: If results differ, the truth likely lies between them (FE upper bound, LDV lower bound for positive effects).
3. Think about selection: Is selection more plausibly based on permanent characteristics (FE) or recent history (LDV)?

Example: Guryan (2004) uses this bracketing reasoning in studying the effects of court-ordered busing on Black high school graduation rates.

Practical Checklist:

1. ✓ FE/DD exploit within-unit variation over time — gives up level comparisons
2. ✓ Always test parallel trends with pre-treatment data when possible
3. ✓ Check for measurement error effects (FE may be attenuated)
4. ✓ Run leads/lags specification — leads should be zero
5. ✓ Try state-specific trends as robustness check
6. ✓ Consider both FE and LDV — they bracket the truth
7. ✓ Watch for composition changes in treatment/control groups