We already know cross-sectional data well. Cross-sectional data covers many individuals at one point in time:

\[ x_i \]

In Econometrics III / Applied Econometrics, we will learn about time series data. Time series data covers one individual at many different points in time:

\[ x_t \]

Today, we will talk briefly about panel data because it is very useful for answering causal questions. In a panel, we follow many individuals over many time periods:

\[ x_{it} \]

Panel data is especially useful because it allows us to control for some unobserved effects without actually observing them.

This is an example of a panel dataset. You can see that we have data on two individuals for two points in time.

Panel data is not as uncommon as you might imagine. Examples for panel data include:

Panel data and models have some useful advantages, such as:

However, there also some potential issues, including:

The simplest model can be obtained by stacking cross-sectional models like this:

\[ \begin{aligned} \begin{pmatrix} \mathbf{y}_1 \\ \mathbf{y}_2 \\ \vdots \\ \mathbf{y}_T \end{pmatrix} &= \begin{pmatrix} \mathbf{X}_1 \\ \mathbf{X}_2 \\ \vdots \\ \mathbf{X}_T \end{pmatrix} \begin{pmatrix} \boldsymbol{\beta}_1 \\ \boldsymbol{\beta}_2 \\ \vdots \\ \boldsymbol{\beta}_T \end{pmatrix} + \begin{pmatrix} \mathbf{u}_1 \\ \mathbf{u}_2 \\ \vdots \\ \mathbf{u}_T \end{pmatrix}. \end{aligned} \]

Alternatively, we can write down the model for a single cross-sectional unit like this:

\[ y_{it}=\boldsymbol{x}_{it}'\boldsymbol{\beta} + u_{it}. \]

This is what we call pooled cross-sections. Coefficients are assumed constant across time and individuals.

In this setting, (pooled) OLS is consistent as long as the assumption \(\mathrm{E}(u_{\textcolor{var(--secondary-color)}{it}}\mid x_{\textcolor{var(--secondary-color)}{it}})=0\) holds.

In many cases, this assumption is problematic. Let’s start discussing this by splitting up the error term in two components, time-invariant heterogeneity between individuals \(\mu_i\) and a time-varying error \(\varepsilon_{it}\):

\[ u_{it} = \textcolor{var(--primary-color)}{\mu_i}+\textcolor{var(--secondary-color)}{\varepsilon_{it}}. \]

There are now two problems with the assumption that \(\mathrm{E}(u_{it}\mid x_{it})=0\), which is equivalent to

\[ \mathrm{E}(u_{it}\mid x_{i1},x_{i2},\dots,x_{iT})=0\text{ for } i= 1,2,\dots,N. \]

We can circumvent this problem by considering individual fixed effects explicitly:

\[ y_{it}=\boldsymbol{x}_{it}'\boldsymbol{\beta} + \mu_i+\varepsilon_{it}. \]

This is equivalent to estimating the model with dummy variables for each individual. These fixed effects capture unobserved individual heterogeneity.

There are two things that these estimators cannot do:

If we have panel data, we can use a difference-in-differences (DiD) approach. We divide our data in four and estimate:

\[ y_{i t} = \alpha + x_{\text{after}} \phi + x_{\text{treated}} \theta + x_{\text{interacted}} \delta + \ldots \]

By comparing and evaluating the difference between the two before-after differences (one for the treatment group, and one for the control group), we can directly obtain the treatment effect, \(\hat{\delta}\).

In the 1800s, London (as well as many other places) was repeatedly hit by waves of a cholera epidemic.

Of course, running an experiment is infeasible in this context. It would requre randomizing households, and allocating clean water to only a subset of them. This was both logistically infeasible and ethically questionable.

In 1849, the following happened:

One water company moved its pipes further upstream, to a location that incidentally was upstream of the main sewage discharge facility. Suddenly, households in the same neighborhoods had access to different qualities of water.

In the end, John Snow collected very convincing evidence for his theory and went on to identify a certain contaminated water pump. The theory, however, was deemed politically unpleasant and was thus not accepted until long after Snow’s death.

For an ideal RDD, we need a few things:

In practice, these requirements are hard to check.

Recall the fundamental problem of causal inference: We cannot observe the counterfactual to our treatment. What we can do is find specific treated observations that are very similar to other untreated observations. We call this procedure matching. It works like this:

This procedure allows us to create a sample with balanced confounders, emulating the balance induced by completely randomized or blocked experiments.

Propensity score matching uses the propensity of being treated for each observation.

• We estimate this propensity, assign a propensity score, and match observations with similar propensity scores. (Note that we reduce all information to one dimension.)
• The method can sometimes induce imbalance rather than remedy it.

Distance matching uses some measure of distance between observations.

• Explaining what “distance” means in this context would require discussing Euclidean geometry.
• Intuitively, you can think distances between points in a scatterplot of covariates.

Coarsened exact matching sorts variables into different bins.

• First, we coarsen covariates, e.g. separating age values into bins.
• Then, we group observations that are in the same set of bins, and discard all sets of bins that only have treated or control observations.

The basic idea of the synthetic control estimator is that we have a treated unit, and multiple untreated units that do not match the characteristics, or trajectory, of the treated unit. So, what we do is to compute a weighted average of untreated units that matches the treated unit (using a data-driven approach).