Week 11: Panel Data Causal Inference

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Last two weeks

• Differences-in-differences designs for dealing with unobserved confounding.

• Identification under Parallel trends

  \[\mathbb{E}[Y_{it}(0) - Y_{it^{\prime}}(0) \mid D_i = 1] - \mathbb{E}[Y_{it}(0) - Y_{it^{\prime}}(0) \mid D_i = 0]\]

• Estimation via first-differences regression (Callaway and Sant’Anna, 2021)

  • Can adjust for time-varying and time-invariant threats to parallel trends.

• Pre-treatment placebo test diagnostics

• Be careful with software defaults!

This week

• In DiD, our identifying assumptions rule out outcome-treatment feedback
  • Treatment is exogenous conditional on observed and unobserved (but structurally constrained) factors
  • But past outcomes do not directly affect present treatment.
• Not uncommon to have dynamic treatment settings where this assumption is violated.
  • Doctors change treatment regimen in response to patient outcomes.
  • Political campaigns adjust their strategy in response to observed poll numbers.
  • Economic growth affects democratization (which affects economic growth)
• In all of these settings, we have \(Y_{t-1}\) affecting treatment \(D_{t}\)
  • And typically also lagged treatment \(D_{t-1}\) affecting current treatment \(D_{t}\)

Review: DiD and Strict Exogeneity

• For this section, we’re going to work with binary treatment \(D_{it}\) observed at each time period \(t\)

  • For simplicity, we’ll consider two time periods generically as \(t\) and \(t-1\)
  • Let \(D_i = \{D_{i1}, D_{i2}, D_{i3}, \dotsc, D_{iT}\}\) denote the entire treatment history for a unit

• In DiD, our parallel trends assumption is a special case of a particular kind of exogeneity/ignorability assumption

  • We assume that treatment history is as-good-as-randomly assigned given observed covariates and some latent factor
  • Let \(\mathbf{X}_i = \{X_{i1}, X_{i2}, X_{i3}, \dotsc, X_{iT}\}\) denote the unit’s observed covariate history
  • Let \(\mathbf{U}_i = \{U_{i1}, U_{i2}, U_{i3}, \dotsc, U_{iT}\}\) denote the unit’s latent factor history

• Strict exogeneity

  \[\{Y_{it}(0), Y_{it}(1) \} \perp\!\!\!\perp D_{i} \mid \mathbf{X}_{i}, \mathbf{U}_i\]

Strict exogeneity

Adapted from Xu (2023) ‘Causal Inference with Time-Series Cross-Sectional Data: A Reflection’

DiD and parallel trends

• If we want to identify the effect of \(D_{t}\) on \(Y_{t}\) (the “instantaneous” effect), via a standard selection-on-observables design, we would need to adjust for both \(X\) and \(U\)

• But here, we’ve supposed that \(U\) is unobserved - can’t control for it directly.

  • We need more assumptions!

• DiD works by making an additional functional form assumption about the latent factor.

  • We assume that we can decompose the latent factor into two additive components: \(U_{it} = \alpha_i + \delta_t\)

• This gives us the classic two-way fixed effect formulation:

  \[Y_{it}(0) = \alpha_i + \delta_t + f(\mathbf{X}_i) + \varepsilon_{it}\]

DiD and parallel trends

• It’s straightforward to see under this functional form assumption and the strict exogeneity assumption, we get parallel trends

  \[\mathbb{E}[Y_{it}(0) - Y_{it-1}(0) \mid D_{it} = 0, \mathbf{X}] = \mathbb{E}[Y_{it}(0) - Y_{it-1}(0) \mid D_{it} = 1, \mathbf{X}] = \delta_{t} - \delta_{t-1}\]

• Under strict exogeneity \(\text{Cov}(\varepsilon_{it}, D_{it}) = 0\)

Sequential ignorability

• But in many panel data settings, ruling out the arrow from \(Y_{t-1}\) to \(D_{t}\) is implausible!

  • We’ll need to make a different assumption
  • Before that though, we need to define the potential outcomes in a new way!

• We now have to consider potential outcomes in terms of the entire treatment history assigned up to time \(t\)

  \[Y_{it}(d_1, d_2, \dotsc, d_t) = Y_{it}(d_{1:t})\]

• We can partition this joint potential outcome into the contemporaneous treatment \(d_t\) and past values \(d_1, d_2, \dotsc, d_{t-1}\)

  \[Y_{it}(d_{1:t}) = Y_{it}(d_{t}; d_{1:t-1})\]

• We’ll define the Contemporaneous Effect of treatment at time \(t\) as:

  \[Y_{it}(1; d_{1:t-1}) - Y_{it}(0; d_{1:t-1}) = Y_{it}(1) - Y_{it}(0)\]

• Later on when we talk about mediation, we’ll introduce other kinds of estimands for cumulative effects over time.

Sequential ignorability

• Identification of causal effects under outcome-treatment feedback can be done under a sequential ignorability assumption (Robins, 1986; Blackwell and Glynn, 2018).

• At each time period, treatment is as-if random conditional on observed covariate and outcome history

  \[\{Y_{it}(1), Y_{it}(0)\} \perp\!\!\!\perp D_{it} \mid X_{it}, Y_{it-1}, D_{it-1}\]

• We can relax this by conditioning on a longer history of outcomes, treatments and covariates.

• Here we’re focusing on the version of sequential ignorability needed for the contemporaneous treatment effect, but can make it more general

  \[\{Y_{is}(d_{1:s}) : s = t, \dotsc, T\} \perp\!\!\!\perp D_{it} \mid X_{it}, Y_{it-1}, D_{it-1}\]

• We’ll cover this more when we talk about mediation

Sequential ignorability

Adapted from Blackwell and Glynn (2018) ‘How to Make Causal Inferences with Time-Series Cross-Sectional Data under Selection on Observables’

Estimation of treatment effects

• Under sequential ignorability, we can motivate estimation of the contemporaneous effect of treatment using an Autoregressive Distributed Lag (ADL) model framework.

  • Adjust for some number of lagged outcomes (autoregressive)
  • Adjust for some number of lagged treatments (distributed lag)

• For example, a one-lag linear model

  \[Y_{it} = X_{it}^\prime\beta + \alpha Y_{it-1} + \tau_0 D_{it} + \tau_1 D_{it-1} + \varepsilon_{it}\]

• If we believe the parametric assumptions behind this model (e.g. constant effects), \(\tau_0\) identifies the average contemporaneous effect of treatment at time \(t\).

• But does \(\tau_1\) identify the effect one period out?

  • No! We have post-treatment bias (Blackwell and Glynn, 2018).
  • This is the Table 2 fallacy all over again.

Sequential ignorability

Adapted from Blackwell and Glynn (2018) ‘How to Make Causal Inferences with Time-Series Cross-Sectional Data under Selection on Observables’

LDV vs. DiD

• We’ll talk about how to estimate these long-term and cumulative effects under sequential ignorability when we get to mediation in a few weeks.
  • The relevant estimands and estimators come from this literature.
  • Future treatment and covariates are mediators of past treatment!
• But let’s consider the simple setting with two time periods and two treatment groups
  • Everyone is under control at time \(t-1\), some units are treated at time \(t\)
• Two possible ways to estimate the treatment effect.
  1. Difference-in-differences - Regress \(Y_{it} - Y_{it-1}\) on \(D_{it}\)
  2. Lagged-DV adjustment - Regress \(Y_{it}\) on \(D_{it}\) and \(Y_{it-1}\)

Controlling for LDV under strict exogeneity

• What happens if we control for the lagged dependent variable under strict exogeneity?
• What we actually want to do is adjust for the expected lagged outcome.
  • But the actual observed outcome contains random error
  • \(Y_{it-1}\) can be high because of the latent factor or the error
• We are controlling for an imperfect proxy of the true confounder
• This measurement error induces a bias due to reversion to the mean
  • If treated units tend to be higher in their outcomes than control (on average), then control units with similar observed outcomes are outliers
  • We’d expect the subsequent outcome to be closer to the mean if there’s independent noise at \(t\) versus \(t-1\)

Simulation: Controlling for LDV

• To see the bias from controlling for lagged \(Y\), consider the following DGP:
  • \(N = 2000\) units, two periods (\(t{-}1\) and \(t\)), true treatment effect \(\tau = 0\)
  • Time-invariant confounder: \(\alpha_i \sim N(0, 1)\)
  • Treatment correlated with confounder: \(D_i \sim \text{Bernoulli}(\text{logit}^{-1}(\alpha_i))\)
  • Outcome at \(t{-}1\): \(Y_{it-1} = \alpha_i + \varepsilon_{it-1}\), where \(\varepsilon_{it-1} \sim N(0, \sigma_\varepsilon^2)\)
  • Outcome at \(t\): \(Y_{it} = \alpha_i + \tau D_i + \varepsilon_{it}\), where \(\varepsilon_{it} \sim N(0, \sigma_\varepsilon^2)\)
• Parallel trends holds by construction: \(\alpha_i\) is time-invariant
• Vary \(\sigma_\varepsilon \in \{0.5, 1, 2, 4, 8\}\) to control how noisy the proxy \(Y_{it-1}\) is for \(\alpha_i\)
• Compare three estimators: simple difference-in-means post-treatment, DiD, and LDV

Simulation: LDV bias from measurement error

set.seed(53703)
N <- 2000
n_sims <- 500
noise_levels <- c(0.5, 1, 2, 4, 8)

sim_results <- map_dfr(noise_levels, function(sigma_e) {
  map_dfr(1:n_sims, function(s) {
    # Time-invariant confounder
    alpha_i <- rnorm(N, 0, 1)
    # Treatment correlated with confounder
    D_i <- rbinom(N, 1, plogis(alpha_i))
    # True treatment effect is ZERO
    beta <- 0
    # Pre and post outcomes: parallel trends holds
    Y_pre <- alpha_i + rnorm(N, 0, sigma_e)
    Y_post <- alpha_i + beta * D_i + rnorm(N, 0, sigma_e)

    # Difference-in-means (biased by alpha_i)
    dim_est <- coef(lm(Y_post ~ D_i))["D_i"]
    # DiD (unbiased)
    did_est <- coef(lm(I(Y_post - Y_pre) ~ D_i))["D_i"]
    # LDV (biased -- errors in variables)
    ldv_est <- coef(lm(Y_post ~ D_i + Y_pre))["D_i"]

    tibble(sigma_e = sigma_e, sim = s,
           `Diff-in-means` = dim_est, DiD = did_est, LDV = ldv_est)
  })
})

sim_summary <- sim_results %>%
  pivot_longer(cols = c(`Diff-in-means`, DiD, LDV),
               names_to = "Estimator", values_to = "estimate") %>%
  group_by(sigma_e, Estimator) %>%
  summarize(mean_est = mean(estimate),
            ci_low = quantile(estimate, 0.025),
            ci_high = quantile(estimate, 0.975), .groups = "drop")

sim_summary$Estimator <- factor(sim_summary$Estimator,
                                levels = c("Diff-in-means", "LDV", "DiD"))

ggplot(sim_summary, aes(x = factor(sigma_e), y = mean_est,
                        color = Estimator, group = Estimator)) +
  geom_point(size = 3, position = position_dodge(width = 0.4)) +
  geom_errorbar(aes(ymin = ci_low, ymax = ci_high),
                width = 0.3, position = position_dodge(width = 0.4)) +
  geom_hline(yintercept = 0, linetype = "dashed") +
  labs(x = expression(paste("Noise in pre-treatment outcome (", sigma[epsilon], ")")),
       y = "Estimate",
       title = "LDV bias under the DiD model (true effect = 0)",
       subtitle = "More noise in Y(pre) = worse proxy for confounder = more residual bias") +
  scale_color_manual(values = c("Diff-in-means" = "gray60",
                                "LDV" = "dodgerblue",
                                "DiD" = "indianred")) +
  theme_bw() + theme(legend.position = "bottom")

Simulation: What if outcomes are autocorrelated?

• In the previous simulation, \(\varepsilon_{it-1}\) and \(\varepsilon_{it}\) are independent — the only thing linking outcomes over time is \(\alpha_i\)
• In practice, outcomes are often autocorrelated: a unit that is high at \(t{-}1\) (beyond \(\alpha_i\)) tends to stay high at \(t\)
• Modified DGP: let \(\varepsilon_{it} = \rho \cdot \varepsilon_{it-1} + \nu_i\) where \(\nu_i \sim N(0, \sigma_\varepsilon^2)\)
  • When \(\rho > 0\), \(Y_{it-1}\) is a better proxy for \(Y_{it}\)’s non-treatment component
  • LDV should perform better because controlling for \(Y_{it-1}\) captures more of the variation
• We fix \(\sigma_\varepsilon = 2\) and vary \(\rho \in \{0, 0.25, 0.5, 0.75, 0.95\}\)

Simulation: Autocorrelation reduces LDV bias

set.seed(53703)
N <- 2000
n_sims <- 500
sigma_e <- 2
rho_levels <- c(0, 0.25, 0.5, 0.75, 0.95)

sim_results_rho <- map_dfr(rho_levels, function(rho) {
  map_dfr(1:n_sims, function(s) {
    alpha_i <- rnorm(N, 0, 1)
    D_i <- rbinom(N, 1, plogis(alpha_i))
    beta <- 0

    eps_pre <- rnorm(N, 0, sigma_e)
    eps_post <- rho * eps_pre + rnorm(N, 0, sigma_e)

    Y_pre <- alpha_i + eps_pre
    Y_post <- alpha_i + beta * D_i + eps_post

    dim_est <- coef(lm(Y_post ~ D_i))["D_i"]
    did_est <- coef(lm(I(Y_post - Y_pre) ~ D_i))["D_i"]
    ldv_est <- coef(lm(Y_post ~ D_i + Y_pre))["D_i"]

    tibble(rho = rho, sim = s,
           `Diff-in-means` = dim_est, DiD = did_est, LDV = ldv_est)
  })
})

sim_summary_rho <- sim_results_rho %>%
  pivot_longer(cols = c(`Diff-in-means`, DiD, LDV),
               names_to = "Estimator", values_to = "estimate") %>%
  group_by(rho, Estimator) %>%
  summarize(mean_est = mean(estimate),
            ci_low = quantile(estimate, 0.025),
            ci_high = quantile(estimate, 0.975), .groups = "drop")

sim_summary_rho$Estimator <- factor(sim_summary_rho$Estimator,
                                    levels = c("Diff-in-means", "LDV", "DiD"))

ggplot(sim_summary_rho, aes(x = factor(rho), y = mean_est,
                            color = Estimator, group = Estimator)) +
  geom_point(size = 3, position = position_dodge(width = 0.4)) +
  geom_errorbar(aes(ymin = ci_low, ymax = ci_high),
                width = 0.3, position = position_dodge(width = 0.4)) +
  geom_hline(yintercept = 0, linetype = "dashed") +
  labs(x = expression(paste("Autocorrelation (", rho, ")")),
       y = "Estimate",
       title = expression(paste("LDV bias with autocorrelated errors (", sigma[epsilon], " = 2, true effect = 0)")),
       subtitle = "More autocorrelation = lagged Y is better proxy = less LDV bias") +
  scale_color_manual(values = c("Diff-in-means" = "gray60",
                                "LDV" = "dodgerblue",
                                "DiD" = "indianred")) +
  theme_bw() + theme(legend.position = "bottom")

Illustration: The Effects of the Shale Shock

• Let’s return to our example of the effect of the “shale shock” on coal county voting for the Republican party (Gazmararian, 2025).
  • Last week we showed concerning evidence of a parallel trends violation - coal-heavy regions were already trending Republican prior to 2008.
  • Extrapolating the trend (triple-differences in time) eliminates the observed effect.
• What if, instead of DiD, we controlled for lagged Republican party vote share in 2004 and 2000.

Lagged DV approach: Setup

dff <- readRDS("assets/data/matched_df.rds")
dff <- dff %>% filter(!is.na(oilgas_prop))

# Create wide-format lagged outcomes
lag_vars <- dff %>%
  select(county_state, year, RepVotesMajorPercent) %>%
  pivot_wider(names_from = year, values_from = RepVotesMajorPercent,
              names_prefix = "Y_")

dff <- dff %>% left_join(lag_vars, by = "county_state")

Lagged DV: Estimates by year

# LDV regressions for each post-treatment year
ldv_years <- c(2008, 2012, 2016, 2020)
ldv_results <- map_dfr(ldv_years, function(yr) {
  df_yr <- dff %>% filter(year == yr)
  fit <- estimatr::lm_robust(
    RepVotesMajorPercent ~ treat + Y_2004 + Y_2000 + oilgas_prop,
    data = df_yr, clusters = county_state, se_type = "stata")
  tidy_fit <- broom::tidy(fit) %>% filter(term == "treat")
  tidy_fit$year <- yr
  tidy_fit
})

ggplot(ldv_results, aes(x = year, y = estimate)) +
  geom_point(size = 3) +
  geom_errorbar(aes(ymin = conf.low, ymax = conf.high), width = 0.5) +
  geom_hline(yintercept = 0, linetype = "dashed") +
  geom_vline(xintercept = 2006, linetype = "dashed", color = "red") +
  labs(x = "Year", y = "Estimate (pp)",
       title = "LDV: Effect of coal county on Republican vote share",
       subtitle = "Controlling for Y[2004], Y[2000], and oil/gas employment") +
  scale_x_continuous(breaks = ldv_years) +
  theme_bw()

DiD: Estimates by year

# DiD regressions for each post-treatment year
did_results <- map_dfr(ldv_years, function(yr) {
  df_yr <- dff %>%
    filter(year == yr) %>%
    mutate(dY = RepVotesMajorPercent - Y_2004)
  fit <- estimatr::lm_robust(
    dY ~ treat + oilgas_prop,
    data = df_yr, clusters = county_state, se_type = "stata")
  tidy_fit <- broom::tidy(fit) %>% filter(term == "treat")
  tidy_fit$year <- yr
  tidy_fit
})

ggplot(did_results, aes(x = year, y = estimate)) +
  geom_point(size = 3) +
  geom_errorbar(aes(ymin = conf.low, ymax = conf.high), width = 0.5) +
  geom_hline(yintercept = 0, linetype = "dashed") +
  geom_vline(xintercept = 2006, linetype = "dashed", color = "red") +
  labs(x = "Year", y = "Estimate (pp)",
       title = "DiD: Effect of coal county on change in Republican vote share",
       subtitle = "Outcome: Y[t] - Y[2004], controlling for oil/gas employment") +
  scale_x_continuous(breaks = ldv_years) +
  theme_bw()

Comparing LDV and DiD

Placebo test: Pre-treatment hold-out

• Let’s construct a placebo test for the lagged DV approach.
  • Because we have many pre-treatment periods, we can apply the LDV approach to pre-treatment outcomes
• Placebo 1: Outcome year 2004, controlling for \(Y_{2000}\) and \(Y_{1996}\)
• Placebo 2: Outcome year 2000, controlling for \(Y_{1996}\) and \(Y_{1992}\)
• Placebo 3: Outcome year 1996, controlling for \(Y_{1992}\) and \(Y_{1988}\)

Placebo: LDV estimates

# Placebo LDV regressions (2 lagged controls, matching main spec)
placebo_ldv_results <- bind_rows(
  # 2004 outcome, controlling for 2000, 1996
  {
    df_yr <- dff %>% filter(year == 2004)
    fit <- estimatr::lm_robust(
      RepVotesMajorPercent ~ treat + Y_2000 + Y_1996 + oilgas_prop,
      data = df_yr, clusters = county_state, se_type = "stata")
    broom::tidy(fit) %>% filter(term == "treat") %>% mutate(year = 2004)
  },
  # 2000 outcome, controlling for 1996, 1992
  {
    df_yr <- dff %>% filter(year == 2000)
    fit <- estimatr::lm_robust(
      RepVotesMajorPercent ~ treat + Y_1996 + Y_1992 + oilgas_prop,
      data = df_yr, clusters = county_state, se_type = "stata")
    broom::tidy(fit) %>% filter(term == "treat") %>% mutate(year = 2000)
  },
  # 1996 outcome, controlling for 1992, 1988
  {
    df_yr <- dff %>% filter(year == 1996)
    fit <- estimatr::lm_robust(
      RepVotesMajorPercent ~ treat + Y_1992 + Y_1988 + oilgas_prop,
      data = df_yr, clusters = county_state, se_type = "stata")
    broom::tidy(fit) %>% filter(term == "treat") %>% mutate(year = 1996)
  }
)

ggplot(placebo_ldv_results, aes(x = year, y = estimate)) +
  geom_point(size = 3) +
  geom_errorbar(aes(ymin = conf.low, ymax = conf.high), width = 0.5) +
  geom_hline(yintercept = 0, linetype = "dashed") +
  labs(x = "Year", y = "Estimate (pp)",
       title = "Placebo test: LDV estimates in pre-treatment periods",
       subtitle = "Each placebo controls for two prior election outcomes + oil/gas share") +
  scale_x_continuous(breaks = c(1996, 2000, 2004)) +
  theme_bw()

Bracketing: Angrist and Pischke (2009)

• Angrist and Pischke (2009, Ch. 5.4) show that LDV and DiD estimates bracket the true causal effect if one of the two identifying assumptions holds.
  • Focus on the simple linear model case - Ding and Li (2019) extend to the non-parametric setting.
• Two-period DiD. All units under control at time \(0\)
  • Assume \(\tau > 0\) (positive effect)
• For exposition, assume time-effects are already removed via differencing and no covariates.

Bracketing: Case 1 – DiD is correct, LDV is misspecified

• Suppose the FE model is the truth:

  \[Y_{it} = \alpha_i + \tau D_{it} + \varepsilon_{it}\]

  where \(\varepsilon_{it}\) is serially uncorrelated and independent of \(\alpha_i\) and \(D_{it}\). Since \(D_{it-1} = 0\): \(Y_{it-1} = \alpha_i + \varepsilon_{it-1}\)

• You mistakenly estimate the LDV regression (controlling for \(Y_{it-1}\) instead of \(\alpha_i\)):

  \[Y_{it} = a + b \cdot Y_{it-1} + \tau^{\text{LDV}} D_{it} + u_{it}\]

Bracketing: Case 1 – FWL decomposition

• By FWL, the LDV estimand is \(\hat{\tau}^{\text{LDV}} \xrightarrow{p} \frac{\text{Cov}(Y_{it}, \tilde{D}_{it})}{\text{Var}(\tilde{D}_{it})}\)

  • \(\tilde{D}_{it} = D_{it} - \hat{\gamma} Y_{it-1}\) is the residual from the auxiliary regression of \(D_{it}\) on \(Y_{it-1}\)

• To evaluate this, substitute \(\alpha_i = Y_{it-1} - \varepsilon_{it-1}\) into the true model:

  \[Y_{it} = \alpha_i + \tau D_{it} + \varepsilon_{it} = (Y_{it-1} - \varepsilon_{it-1}) + \tau D_{it} + \varepsilon_{it}\]

  \[\Rightarrow Y_{it} = Y_{it-1} + \tau D_{it} + (\varepsilon_{it} - \varepsilon_{it-1})\]

Bracketing: Case 1 – Deriving the bias

• Substitute in and use properties of covariances

  \[\frac{\text{Cov}(Y_{it}, \tilde{D}_{it})}{\text{Var}(\tilde{D}_{it})} = \frac{\text{Cov}(Y_{it-1} + \tau D_{it} + \varepsilon_{it} - \varepsilon_{it-1},\; \tilde{D}_{it})}{\text{Var}(\tilde{D}_{it})}\]

• \(\text{Cov}(Y_{it-1}, \tilde{D}_{it}) = 0\) by construction (FWL residualizes out \(Y_{it-1}\))

• \(\text{Cov}(D_{it}, \tilde{D}_{it}) = \text{Var}(\tilde{D}_{it})\)

• \(\text{Cov}(\varepsilon_{it}, \tilde{D}_{it}) = 0\) since \(\varepsilon_{it} \perp\!\!\!\perp (D_{it}, Y_{it-1})\)

• But \(\text{Cov}(\varepsilon_{it-1}, \tilde{D}_{it}) = \text{Cov}(\varepsilon_{it-1}, D_{it}) - \hat{\gamma}\text{Cov}(\varepsilon_{it-1}, Y_{it-1})\)

  • And since \(Y_{it-1} = \alpha_i + \varepsilon_{it-1}\)…
  • \(\text{Cov}(\varepsilon_{it-1}, \tilde{D}_{it}) = -\hat{\gamma}\sigma^2_{\varepsilon}\)

• So: \(\hat{\tau}^{\text{LDV}} \xrightarrow{p} \tau + \frac{\hat{\gamma} \sigma^2_\varepsilon}{\text{Var}(\tilde{D}_{it})}\), with bias having the same sign as \(\hat{\gamma}\) (the sign of selection)

Bracketing: Case 1 – Why is LDV biased?

• \(Y_{it-1} = \alpha_i + \varepsilon_{it-1}\) is a noisy proxy for the confounder \(\alpha_i\)
  • Controlling for a noisy proxy does not fully remove confounding
• With positive selection (high outcome \(\leadsto\) more likely to be treated) (\(\hat{\gamma} > 0\))
  • LDV overestimates \(\tau\)
• With negative selection (\(\hat{\gamma} < 0\))
  • LDV underestimates \(\tau\)

Bracketing: Case 2 – LDV is correct, DiD is misspecified

• Now suppose the LDV model is the truth:

  \[Y_{it} = \alpha + \theta Y_{it-1} + \tau D_{it} + \varepsilon_{it}\]

• Where \(\varepsilon_{it}\) is serially uncorrelated, \(0 < \theta < 1\) (stationary)

• You mistakenly estimate the first-differenced regression (no control for \(Y_{it-1}\)):

  \[\Delta Y_{it} = a + \tau^{\text{DiD}} D_{it} + u_{it}\]

  where \(\Delta Y_{it} = Y_{it} - Y_{it-1}\) and \(D_{it-1} = 0\) for everyone

Bracketing: Case 2 – FWL decomposition

• The DiD estimand is \(\hat{\tau}^{\text{DiD}} \xrightarrow{p} \frac{\text{Cov}(\Delta Y_{it}, D_{it})}{\text{Var}(D_{it})}\)

• Subtract \(Y_{it-1}\) from both sides of the true model:

  \[Y_{it} - Y_{it-1} = \alpha + (\theta - 1)Y_{it-1} + \tau D_{it} + \varepsilon_{it}\]

• So \(\Delta Y_{it} = \alpha + (\theta - 1)Y_{it-1} + \tau D_{it} + \varepsilon_{it}\). Substituting:

  \[\frac{\text{Cov}(\Delta Y_{it}, D_{it})}{\text{Var}(D_{it})} = \frac{\text{Cov}(\alpha + (\theta - 1)Y_{it-1} + \tau D_{it} + \varepsilon_{it}, D_{it})}{\text{Var}(D_{it})} \]

  \[\frac{\text{Cov}(\Delta Y_{it}, D_{it})}{\text{Var}(D_{it})} = \tau + (\theta - 1)\frac{\text{Cov}(Y_{it-1}, D_{it})}{\text{Var}(D_{it})} + \frac{\text{Cov}(\varepsilon_{it}, D_{it})}{\text{Var}(D_{it})}\]

• \(\text{Cov}(\varepsilon_{it}, D_{it}) = 0\) by assumption (LDV model has no unobserved confounding)

Bracketing: Case 2 – Deriving the bias

• Therefore:

  \[\hat{\tau}^{\text{DiD}} \xrightarrow{p} \tau + (\theta - 1)\frac{\text{Cov}(Y_{it-1}, D_{it})}{\text{Var}(D_{it})}\]

• The bias is \((\theta - 1)\frac{\text{Cov}(Y_{it-1}, D_{it})}{\text{Var}(D_{it})}\)

• The bias has the opposite sign from the selection:

  • With positive selection (\(\text{Cov}(Y_{it-1}, D_{it}) > 0\)) and \(\theta < 1\): bias is negative → DiD underestimates
  • With negative selection: bias is positive → DiD overestimates

• Under this model, LDV is unbiased: it correctly controls for \(Y_{it-1}\)

Bracketing

• Combining both cases with positive selection (\(\text{Cov}(\alpha_i, D_i) > 0\)):

  • If strict exogeneity is correct: LDV overestimates, DiD is exact
  • If sequential ignorability is correct: DiD underestimates, LDV is exact

• The true effect is bracketed between the two estimates if one of these two assumptions is true.

• This is a useful result, but important to be aware of its limitations

  • It guarantees nothing if neither assumption is true!

• In many cases, we’re skeptical of parallel trends but we don’t think sequential ignorability is right either

  • Rather, we think the unobserved latent factor structure might be more complicated than \(U_{it} = \alpha_i + \delta_t\)
  • What do we do then?

The Synthetic Control Method

• Comparative case studies in the social sciences try to assess the impact of some event by comparing the case of interest to some unaffected units
  • We ideally want to pick units that are similar enough that they share the same latent characteristics shaping the evolution of the outcome.
• The Synthetic Control Method (SCM) builds on this intuition (Abadie and Gardeazabal, 2003; Abadie, Diamond, and Hainmueller, 2010).
  • What if instead of using a single comparison, we use a weighted average of those units.
  • Find weights on the control units that reproduce the pre-treatment outcome trajectory of the treated unit
  • Compare the observed outcome trajectory to the synthetic control average.
• Justified under two different outcome models
  • Under sequential ignorability, we get an unbiased estimator (because past outcomes are direct confounders)
  • Under a latent factor model, the bias goes away as the number of time periods gets large.

SCM: Setup and Notation

• Observe outcomes \(Y_{it}\) for units \(i = 1, \dotsc, J+1\) over periods \(t = 1, \dotsc, T\)

  • Let \(T_0\) denote the number of pre-treatment periods, \(T_1\) the number of post-treatment
  • Unit \(i = 1\) is the treated unit, exposed to treatment starting at \(T_0 + 1\)
  • Units \(i = 2, \dotsc, J+1\) are donor units (never treated)

• We want to estimate:

  \[\tau_{1t} = Y_{1t}(1) - Y_{1t}(0) \quad \text{for } t > T_0\]

• We define a set of weights on the donor units \(\mathbf{W} = (w_2, \dotsc, w_{J+1})\) with \(w_j \geq 0\) and \(\sum_j w_j = 1\)

• Estimate the effect by comparing the observed outcome to the imputed counterfactual

  \[\hat{\tau_{1t}} = Y_{1t} - \sum_{j=2}^{J+1} w_j Y_{jt}\]

SCM: The data-generating process

• The SCM is typically motivated by an underlying latent factor model for the outcome

  \[Y_{it}(0) = \delta_t + \mathbf{\theta}_t \mathbf{Z}_i + \boldsymbol{\lambda}_t' \boldsymbol{\mu}_i + \varepsilon_{it}\]

• \(\mathbf{Z}_i\) are the observed covariates (with time-varying coefficients \(\mathbf{\theta}_t\)).

• \(\boldsymbol{\lambda}_t\) are \(F\)-dimensional time-varying factors and \(\boldsymbol{\mu}_i\) are unit-specific loadings

• This is a more general model of latent unobserved confounding than DiD

  • In DiD, there is a single common time trend across all factors \(\boldsymbol{\lambda}_t = \lambda\)
  • The latent factor model allows for some number of varying time-trends across units (elements of \(\boldsymbol{\lambda}_t\)) that apply to different units (weights dictated by \(\boldsymbol{\mu}_i\)).

SCM: Choosing the weights

• The goal of the synthetic control method is to find weights such that the weighted average of donor units reproduces the covariates and the pre-treatment trajectory of the treated unit

  \[\sum_{j=2}^{J+1} w^*_j Y_{jt} = Y_{1t} \quad \text{for } t \in \{1, 2, \dotsc, T_0\}\]

  \[\sum_{j=2}^{J+1} w^*_j \mathbf{Z}_j = \mathbf{Z}_{1}\]

• For notational simplicity, we’ll denote the \(K \times J+1\) matrix of combined covariates and pre-treatment outcomes as \(\mathbf{X}\)

  • \(\mathbf{X}_1\) is the \(K x 1\) vector for the treated unit
  • \(\mathbf{X}_0\) is the \(K x J\) matrix for the control units.

• The ideal synthetic control has weights weights \(\mathbf{W}^*\) such that \(\mathbf{X}_1 = \mathbf{X}_0 \mathbf{W}^*\)

SCM: Bias

• Supposing that we find \(\mathbf{W}^*\), what is the error in our imputed counterfactual?

  \[Y_{1t}(0) - \sum_{j=2}^{J+1} w^*_j Y_{jt}\]

• Abadie, Diamond and Hainmueller (2010) show that under the latent factor model, the expected error goes to zero…

  • …when the number of pre-treatment periods is large…
  • …relative to the size of the pre-treatment shocks!

• Intuition: Remember our earlier errors-in-variables example when we controlled for a lagged dependent variable!

  • The lagged outcomes are proxies for the latent factor - the less noisy the proxy, the better it reproduces the true unobserved latent factor.

• Under an autoregressive outcome model, the bias is zero!

  • “Sequential ignorability” - past \(Y\) directly affects future \(Y\).

SCM: Estimating the weights

• In practice, we can only get \(\mathbf{X}_1 \approx \mathbf{X}_0 \mathbf{W}^*\)

  • How do we find \(\mathbf{W}^*\)?

• We solve a constrained minimization problem that minimizes a distance metric

• For example, the euclidean norm:

  \[||\mathbf{X}_1 - \mathbf{X}_0 \mathbf{W}^*|| = \sqrt{\sum_{h=1}^K v_h(X_{h1} - w_2 X_{h2} - w_3 X_{h3} - \dotsc - w_{J+1}X_{hJ+1})^2}\]

• We impose constraints:

  • \(\sum_{j=2}^{J+1} w_j = 1\) Weights sum to 1
  • \(w_j \ge 0 \quad \forall j \in \{2, 3, \dotsc, J+1\}\) Weights are non-negative

• Note that we also get to choose how much importance to put on each dimension (covariate) \(\mathbf{V} = \{v_1, v_2, \dotsc, v_K\}\)

  • Abadie, Diamond and Hainmueller (2010) use an out-of-sample validation approach against the pre-treatment outcomes to choose an optimal \(\mathbf{V}\)

SCM: Notes on the weights

• The non-negativity and sum to 1 have some useful properties:

  • Sparse - most weights are 0
  • Interpretable - we can characterize the precise contributions of each element of the donor pool to the synthetic control
  • Avoid extrapolation

• But there are problems!

  • If the treated unit is outside the convex hull of the controls, it’s impossible to reproduce the pre-treatment trajectory!

• In general, the bias \(\to 0\) results are derived under perfect fit - if the synthetic control is a poor match, bias can be huge!

• Possible solutions

  • Add an intercept (Doudchenko and Imbens, 2017; Ferman and Pinto, 2021)
  • Allow for negative weights (Doudchenko and Imbens, 2017)
  • Add an outcome model to correct for imperfect fit (Ben-Michael, Feller and Rothstein, 2021)

Application: Basque Country Terrorism

• Abadie and Gardeazabal (2003): Effect of ETA terrorism on the Basque Country’s GDP per capita
  • Treatment: onset of political terrorism in the late 1960s (they use ~1970 as treatment)
  • Donor pool: 16 other Spanish regions
  • Outcome: real GDP per capita (thousands of 1986 USD)
  • Time: 1955-1997
• Replication example in the Synth package

Basque Country: Data Preparation

library(Synth)
data(basque)

# Prepare data for Synth
dataprep.out <- dataprep(
  foo = basque,
  predictors = c("school.illit", "school.prim", "school.med",
                 "school.high", "school.post.high", "invest"),
  predictors.op = "mean",
  time.predictors.prior = 1964:1969,
  special.predictors = list(
    list("gdpcap", 1960:1969, "mean"),
    list("sec.agriculture", seq(1961, 1969, 2), "mean"),
    list("sec.energy", seq(1961, 1969, 2), "mean"),
    list("sec.industry", seq(1961, 1969, 2), "mean"),
    list("sec.construction", seq(1961, 1969, 2), "mean"),
    list("sec.services.venta", seq(1961, 1969, 2), "mean"),
    list("sec.services.nonventa", seq(1961, 1969, 2), "mean"),
    list("popdens", 1969, "mean")
  ),
  dependent = "gdpcap",
  unit.variable = "regionno",
  unit.names.variable = "regionname",
  time.variable = "year",
  treatment.identifier = 17,  # Basque Country
  controls.identifier = c(2:16, 18),  # All other regions (excluding Spain aggregate = 1)
  time.optimize.ssr = 1960:1969,
  time.plot = 1955:1997
)

Basque Country: Fitting the Synthetic Control

# Run the synth optimization
synth.out <- synth(data.prep.obj = dataprep.out, method = "BFGS")

# Display the weights
synth.tables <- synth.tab(dataprep.res = dataprep.out, synth.res = synth.out)
cat("Donor weights (non-zero):\n")

Donor weights (non-zero):

w <- synth.tables$tab.w
print(w[w$w.weights > 0.01, ])

   w.weights            unit.names unit.numbers
10     0.851              Cataluna           10
14     0.149 Madrid (Comunidad De)           14

Basque Country: Synthetic vs. Actual

# Extract path data
years <- dataprep.out$tag$time.plot
Y_treat <- dataprep.out$Y1plot
Y_synth <- dataprep.out$Y0plot %*% synth.out$solution.w

plot_df <- data.frame(
  year = years,
  Treated = as.numeric(Y_treat),
  Synthetic = as.numeric(Y_synth)
) %>%
  pivot_longer(cols = c(Treated, Synthetic), names_to = "Unit", values_to = "gdpcap")

ggplot(plot_df, aes(x = year, y = gdpcap, color = Unit, linetype = Unit)) +
  geom_line(linewidth = 1.2) +
  geom_vline(xintercept = 1970, linetype = "dashed", color = "gray40") +
  annotate("text", x = 1971, y = 3, label = "Terrorism\nonset", hjust = 0, size = 3.5) +
  labs(x = "Year", y = "Real per capita GDP\n(1986 USD, thousands)",
       title = "Basque Country vs. Synthetic Basque Country",
       subtitle = "Abadie & Gardeazabal (2003) — Effect of ETA terrorism on GDP") +
  scale_color_manual(values = c("Treated" = "black", "Synthetic" = "firebrick")) +
  scale_linetype_manual(values = c("Treated" = "solid", "Synthetic" = "dashed")) +
  theme_bw() + theme(legend.position = "bottom")

Basque Country: Treatment Effect (Gap Plot)

gap <- as.numeric(Y_treat) - as.numeric(Y_synth)
gap_df <- data.frame(year = years, gap = gap)

ggplot(gap_df, aes(x = year, y = gap)) +
  geom_line(linewidth = 1.2) +
  geom_hline(yintercept = 0, linetype = "dashed") +
  geom_vline(xintercept = 1970, linetype = "dashed", color = "gray40") +
  annotate("text", x = 1971, y = 0.4, label = "Terrorism onset", hjust = 0, size = 3.5) +
  labs(x = "Year", y = "Gap in real per capita GDP\n(Treated − Synthetic)",
       title = "Estimated effect of terrorism on Basque Country GDP",
       subtitle = "Negative gap = terrorism reduced GDP relative to synthetic control") +
  theme_bw()

SCM: Inference

• With a single treated unit, standard inference is not straightforward. Abadie et al. (2010) propose a permutation testing approach:
  • Apply SCM to each donor unit as if it were treated
  • If the treated unit’s gap is unusually large relative to these “placebo” gaps, the effect is unlikely due to chance
  • Test statistic: post/pre RMSPE ratio
  • Common practice to drop controls with egregiously worse pre-treatment fit compared to treated unit.
• Recent work in statistics moves beyond this:
  • “Conformal inference” approach in Chernozhukov, Wüthrich, and Zhu (2019)

Basque Country: Permutation tests

# Run placebo tests for each control region
control_ids <- c(2:16, 18)
placebo_gaps <- list()

for (ctrl_id in control_ids) {
  donor_ids <- setdiff(c(2:16, 18), ctrl_id)

  tryCatch({
    dp <- dataprep(
      foo = basque,
      predictors = c("school.illit", "school.prim", "school.med",
                     "school.high", "school.post.high", "invest"),
      predictors.op = "mean",
      time.predictors.prior = 1964:1969,
      special.predictors = list(
        list("gdpcap", 1960:1969, "mean"),
        list("sec.agriculture", seq(1961, 1969, 2), "mean"),
        list("sec.energy", seq(1961, 1969, 2), "mean"),
        list("sec.industry", seq(1961, 1969, 2), "mean"),
        list("sec.construction", seq(1961, 1969, 2), "mean"),
        list("sec.services.venta", seq(1961, 1969, 2), "mean"),
        list("sec.services.nonventa", seq(1961, 1969, 2), "mean"),
        list("popdens", 1969, "mean")
      ),
      dependent = "gdpcap",
      unit.variable = "regionno",
      unit.names.variable = "regionname",
      time.variable = "year",
      treatment.identifier = ctrl_id,
      controls.identifier = donor_ids,
      time.optimize.ssr = 1960:1969,
      time.plot = 1955:1997
    )

    so <- synth(data.prep.obj = dp, method = "BFGS")

    y1 <- as.numeric(dp$Y1plot)
    y0 <- as.numeric(dp$Y0plot %*% so$solution.w)
    placebo_gaps[[as.character(ctrl_id)]] <- data.frame(
      year = 1955:1997, gap = y1 - y0, unit = ctrl_id
    )
  }, error = function(e) {
    # Skip units where optimization fails
  })
}

placebo_df <- do.call(rbind, placebo_gaps)

# Add treated unit
treated_gap_df <- data.frame(year = years, gap = gap, unit = 17)

Basque Country: Permutation tests

ggplot() +
  geom_line(data = placebo_df, aes(x = year, y = gap, group = unit),
            color = "gray70", alpha = 0.6) +
  geom_line(data = treated_gap_df, aes(x = year, y = gap),
            color = "black", linewidth = 1.2) +
  geom_vline(xintercept = 1970, linetype = "dashed", color = "gray40") +
  geom_hline(yintercept = 0, linetype = "dashed") +
  labs(x = "Year", y = "Gap in real per capita GDP",
       title = "Placebo tests: Basque Country (black) vs. donor regions (gray)",
       subtitle = "Each gray line = SCM applied to a donor region as if it were treated") +
  theme_bw()

Permutation Tests: Dropping Poor Fits

# Compute pre-treatment RMSPE for each unit
treated_pre_rmspe <- sqrt(mean((treated_gap_df %>% filter(year < 1970))$gap^2))

placebo_pre_rmspe <- placebo_df %>%
  filter(year < 1970) %>%
  group_by(unit) %>%
  summarize(pre_rmspe = sqrt(mean(gap^2))) %>%
  ungroup()

# Keep only units with pre-RMSPE <= 5x the treated unit
keep_units <- placebo_pre_rmspe %>%
  filter(pre_rmspe <= 5 * treated_pre_rmspe) %>%
  pull(unit)

placebo_df_trimmed <- placebo_df %>% filter(unit %in% keep_units)

n_dropped <- n_distinct(placebo_df$unit) - length(keep_units)

ggplot() +
  geom_line(data = placebo_df_trimmed, aes(x = year, y = gap, group = unit),
            color = "gray70", alpha = 0.6) +
  geom_line(data = treated_gap_df, aes(x = year, y = gap),
            color = "black", linewidth = 1.2) +
  geom_vline(xintercept = 1970, linetype = "dashed", color = "gray40") +
  geom_hline(yintercept = 0, linetype = "dashed") +
  labs(x = "Year", y = "Gap in real per capita GDP",
       title = paste0("Placebo tests: Dropping donors with pre-RMSPE > 5x treated (",
                      n_dropped, " dropped)"),
       subtitle = "Basque Country (black) vs. donor regions with adequate pre-treatment fit (gray)") +
  theme_bw()

Permutation Tests: RMSPE Ratios

# Compute post/pre RMSPE ratios
compute_rmspe_ratio <- function(gap_df, treatment_year = 1970) {
  pre <- gap_df %>% filter(year < treatment_year)
  post <- gap_df %>% filter(year >= treatment_year)
  rmspe_pre <- sqrt(mean(pre$gap^2))
  rmspe_post <- sqrt(mean(post$gap^2))
  rmspe_post / rmspe_pre
}

# Treated unit ratio
treated_ratio <- compute_rmspe_ratio(treated_gap_df)

# Placebo ratios
placebo_ratios <- placebo_df %>%
  group_by(unit) %>%
  group_modify(~ tibble(ratio = compute_rmspe_ratio(.x))) %>%
  ungroup()

all_ratios <- bind_rows(
  placebo_ratios,
  tibble(unit = 17, ratio = treated_ratio)
) %>%
  mutate(is_treated = unit == 17)

# Compute p-value
pval <- mean(all_ratios$ratio >= treated_ratio)

ggplot(all_ratios, aes(x = ratio, fill = is_treated)) +
  geom_histogram(bins = 15, color = "white", alpha = 0.8) +
  geom_vline(xintercept = treated_ratio, linetype = "dashed", color = "red", linewidth = 1) +
  scale_fill_manual(values = c("FALSE" = "gray70", "TRUE" = "black"),
                    labels = c("Donor regions", "Basque Country"),
                    name = "") +
  labs(x = "Post/Pre RMSPE Ratio",
       y = "Count",
       title = "Distribution of RMSPE ratios: Permutation inference",
       subtitle = paste0("Basque Country ratio = ", round(treated_ratio, 2),
                         " | p-value = ", round(pval, 3))) +
  theme_bw() + theme(legend.position = "bottom")

Staggered Adoption SCM

• Conventional SCM is designed for one treated unit — what if multiple units are treated?

  • What should we weight our control pool to - each unit separately or the average of the units?

• We might get perfect balance for the average of the units but terrible fit for individual treated units!

• Ben-Michael, Feller and Rothstein (2022) show that the bias is a combination of these two imbalances.

  • Propose a partial pooling approach that minimizes a combination of the two.

• Implemented in the augsynth R package (along with their outcome-augmented synthetic control)

Application: Shale Shock and Republican Voting

• Let’s apply the augmented/multi-unit synthetic control to the Gazmararian (2025) shale shock data
  • Earlier, we saw that DiD and LDV gave different estimates, and placebo tests raised concerns
  • Is SCM the solution?
• Review of the setup:
  • 116 treated coal counties, 97 control counties
  • Treatment onset: 2008 (shale gas boom undermines coal industry)
  • Outcome: Republican vote share
  • Pre-treatment periods: 1972–2004 (8 election cycles)
  • Post-treatment periods: 2008–2020 (4 election cycles)

multisynth: Average Effect Across Treated Units

library(augsynth)

# Use multisynth for the multi-unit case
# multisynth infers treatment timing from the binary indicator
msyn <- multisynth(
  RepVotesMajorPercent ~ treated,
  unit = county_state, time = year,
  data = dff
)

msyn_summ <- summary(msyn)

# Extract average ATT for plotting
avg_att <- msyn_summ$att %>%
  filter(Level == "Average")

ggplot(avg_att, aes(x = Time, y = Estimate)) +
  geom_point(size = 3) +
  geom_errorbar(aes(ymin = lower_bound, ymax = upper_bound), width = 0.3) +
  geom_hline(yintercept = 0, linetype = "dashed") +
  geom_vline(xintercept = -0.5, linetype = "dashed", color = "red") +
  labs(x = "Time relative to treatment (election cycles)",
       y = "Estimated ATT (pp)",
       title = "Multisynth: Effect of shale shock on Republican vote share",
       subtitle = "Average across treated coal counties (partially pooled SCM)") +
  theme_bw()

Placebo testing

• We’ve fit the synthetic control model to minimize pre-treatment outcome discrepancies.
  • A perfect synthetic control will reproduce the trajectory exactly
  • But this doesn’t mean that our estimator is unbiased - especially if we have a short panel.
  • How do we assess whether the bias is small?
    • Perfect pre-treatment fit is no longer a valid placebo test!
• We can use a placebo test approach where we backdate the treatment to an earlier period and check whether the synthetic control produces spurious “effects” in held-out pre-treatment periods
  • Same intuition as our discussion last week - we want our placebo tests to involve held-out comparisons.

Backdating falsification tests

# In-time falsification: backdate treatment to 2000 and 1996
# Fit SCM using only pre-placebo data, check for "effects" in held-out periods

placebo_years <- c(1996, 2000, 2004)

falsification_results <- list()

for (placebo_yr in placebo_years) {
  # Create dataset: only pre-2008 data, with treatment backdated
  falsification_df <- dff %>%
    filter(year < 2008) %>%
    mutate(placebo_treat = as.integer(treat == 1 & year >= placebo_yr))

  tryCatch({
    plac_fit <- multisynth(
      RepVotesMajorPercent ~ placebo_treat,
      unit = county_state, time = year,
      data = falsification_df,
    )

    plac_summ <- summary(plac_fit)
    plac_att <- plac_summ$att %>%
      filter(Level == "Average") %>%
      mutate(placebo_year = placebo_yr)

    falsification_results[[as.character(placebo_yr)]] <- plac_att
  }, error = function(e) {
    cat("Error for placebo year", placebo_yr, ":", conditionMessage(e), "\n")
  })
}

all_results <- bind_rows(
  do.call(rbind, falsification_results)
) %>%
  mutate(placebo_label = paste0("Placebo treatment = ", placebo_year))

ggplot(all_results, aes(x = Time, y = Estimate,
                         color = factor(placebo_year))) +
  geom_point(size = 2.5) +
  geom_errorbar(aes(ymin = lower_bound, ymax = upper_bound), width = 0.3) +
  geom_hline(yintercept = 0, linetype = "dashed") +
  geom_vline(xintercept = -0.5, linetype = "dotted") +
  facet_wrap(~ placebo_label, scales = "free_x") +
  labs(x = "Time relative to (placebo) treatment",
       y = "Estimated ATT (pp)",
       title = "Placebo tests: backdated treatment vs. actual",
       subtitle = "Placebo treatments should show no effect in held-out pre-2008 periods") +
  scale_color_manual(values = c("1996" = "steelblue", "2000" = "darkorange",
                                 "2004" = "black")) +
  theme_bw() + theme(legend.position = "none")

Conclusion

• Causal inference in time-series data is hard!

  • Even the estimands can get tricky - we’ll come back to this again when we talk about mediation

• The core problem centers around how we deal with unobserved confounding and the role that past outcomes play in identification/estimation

• Three scenarios:

  • Unobserved confounding but simple functional form (DiD)
    • Adjust via differencing - works in short panels
  • Observed confounding driven by past \(Y\)
    • Adjust by controlling for past \(Y\) - also fine in short panels
  • Unobserved confounding more complex than DiD
    • Adjust for past \(Y\) to indirectly control for the latent factor - need many pre-treatment periods!

Next week

• The last of the “holy trinity” - regression discontinuity designs

• What happens when we have arbitrary unobserved confounding…

  • …but treatment is assigned via a threshold

• In this case, even if treatment-outcome are confounded, that confounding might be negligible in the window around the threshold!

• Two ways to think about this

  • “As-if-random” assignment at the cut-off
  • Continuity in potential outcomes at the cut-off

• Estimation by extrapolation to the threshold.

  • Works best when we have lots of units near the cut-off.