## Abstract

The propensity score methodology has become quite common in applied research in the last 10 years, and criminology is no exception to this growing trend. It offers a potentially powerful way to estimate the treatment effect of some intervention on behavior when the receipt of treatment arises in a nonrandom way – this is the selection problem. It does so by creating synthetic “experimental” and “control” groups that are equivalent on a large number of potential confounding variables. In this chapter, we first introduce the counterfactual framework on which the propensity score method is based and define the average treatment effect. We then outline technical issues that must be addressed when the propensity score method is used in practice, including estimation of the propensity score, demonstration of covariate balance, and estimation of the treatment effect of interest. To provide a step-by-step example of the method, we appeal to the relationship between employment and substance use in adolescence. Following a brief review of research in criminology and related disciplines that employ the propensity score methodology, we offer a number of guidelines for use of the technique.

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## Notes

- 1.
- 2.
Notice that the counterfactual definition of causality requires that the individual occupy two states at the same time, not two different states at two different times. If the latter condition held, panel data with a time-varying treatment condition would suffice to estimate a causal effect of treatment. In the marriage example, the period(s) in which the individual is not married would be the counterfactual for the period(s) in which the same individual is married.

- 3.
In this chapter, we will be mostly concerned with estimation of ATE rather that its constituents, ATT and ATU.

- 4.
Because it renders treatment ignorable, randomization is sufficient to identify the average treatment effect in the following manner:

$$\begin{array}{l} \mathrm{ATE} = \mathrm{E}\left (\left.{Y }_{i}^{1}\right \vert {T}_{i} = 1\right ) -\mathrm{E}\left (\left.{Y }_{i}^{0}\right \vert {T}_{i} = 0\right ) \\ \qquad \ = \mathrm{E}\left (\left.{Y }_{i}\right \vert {T}_{i} = 1\right ) -\mathrm{E}\left (\left.{Y }_{i}\right \vert {T}_{i} = 0\right ) \end{array}$$Notice that this is simply the mean difference in the outcome for treated and untreated individuals in the target population, as the potential outcomes notation in the first equality can be removed. The second equality necessarily follows because treatment assignment independent of potential outcomes ensures that:

$$\mathrm{E}\left (\left.{Y }_{i}^{1}\right \vert {T}_{ i} = 1\right ) = E\left (\left.{Y }_{i}^{1}\right \vert {T}_{ i} = 0\right ) = E\left (\left.{Y }_{i}\right \vert {T}_{i} = 1\right )$$and

$$\mathrm{E}\left (\left.{Y }_{i}^{0}\right \vert {T}_{ i} = 1\right ) = E\left (\left.{Y }_{i}^{0}\right \vert {T}_{ i} = 0\right ) = E\left (\left.{Y }_{i}\right \vert {T}_{i} = 0\right )$$As an interesting aside, in the case of a randomized experiment, it is also the case that ATT and ATU are equivalent to ATE by virtue of these equalities.

- 5.
To be perfectly accurate, randomization may in fact produce imbalance, but the imbalance is attributable entirely to chance. However, asymptotically (i.e., as the sample size tends toward infinity) the expected imbalance approaches zero.

- 6.
Aside from ethical and practical concerns, this experiment would be unable to assess the effect of marriage as we know it, as marriages entered into on the basis of a coin flip would likely have very different qualities than those freely chosen.

- 7.
Researchers differ in their preferences for how exhaustive the treatment status model should be. In a

*theoretically informed model*, the researcher includes only a vector of variables that are specified a priori in the theory or theories of choice. In a*kitchen sink model*, the researcher includes as many variables as are available in the dataset. In our view, a theoretically informed model is appealing only to the extent that it achieves balance on confounders that are excluded from the treatment status model but would have been included in a kitchen sink model. - 8.
Some researchers also include functions of the confounders in the treatment status model, for example, quadratic and interaction terms.

- 9.
A useful sensitivity exercise is to estimate treatment effects using a number of different bandwidths to determine stability of the estimates. With smaller bandwidths, common support shrinks and fewer cases are retained. This alters the nature of the estimated treatment effect, particularly if a large number of cases are excluded. This can be dealt with by simply acknowledging that the estimated effect excludes certain kinds of cases, and these can be clearly described since the dropped cases are observed.

- 10.
Where substantive significance is as important as statistical significance, the standardized bias formula can also be used to estimate an effect size for the treatment effect estimate (see Cohen, 1988).

- 11.
In practice, Wooldridge (2002) recommends augmenting the regression model in the following way:

$${Y }_{i} = {\alpha }^{{\prime}} + {\beta }^{{\prime}}{T}_{ i} + {\gamma }^{{\prime}}P({x}_{ i}) + {\delta }^{{\prime}}{T}_{ i}\left [P({x}_{i}) -\bar{ P}({x}_{i})\right ] + {e}_{i}^{{\prime}}$$where \(\bar{P}({x}_{i})\) represents the mean propensity score for the target population and ATE is estimated the same way, but by using β

^{′}in place of β. - 12.
Nearest neighbor matching can be done with or without replacement.

*Matching without replacement*means that once an untreated case has been matched to a treated case, it is removed from the candidates for matching. This may lead to poor matches when the distribution of propensity scores is quite different for the treated and untreated groups. Matching without replacement also requires that cases be randomly sorted prior to matching, as sort order can affect matches when there are cases with equal propensity scores.*Matching with replacement*allows an untreated individual to serve as the counterfactual for multiple treated individuals. This allows for better matches, but reduces the number of untreated cases used to create the treatment effect estimate, which increases the variance of the estimate (Smith and Todd 2005). As with the choice of the number of neighbors, one has to balance concerns of bias and efficiency. - 13.
When there are many cases at the boundaries of the propensity score distribution, it may be useful to generalize kernel matching to include a linear term; this is called local linear matching. Its main advantage over kernel matching is that it yields more accurate estimates at boundary points in the distribution of propensity scores and it deals better with different data densities (Smith and Todd 2005).

- 14.
Apel et al. (2006, 2007, 2008); Bachman et al. (1981, 2003); Bachman and Schulenberg (1993); Gottfredson (1985); Greenberger et al. (1981); Johnson (2004); McMorris and Uggen (2000); Mihalic and Elliott (1997); Mortimer (2003); Mortimer et al. (1996); Paternoster et al. (2003); Ploeger (1997); Resnick et al. (1997); Safron et al. (2001); Staff and Uggen (2003); Steinberg and Dornbusch (1991); Steinberg et al. (1982, 1993); Tanner and Krahn (1991).

- 15.
If we select the sample treatment probability as the classification threshold, 71.8 percent of the sample is correctly classified from the model shown in Table26.1.

- 16.
The sign of the standardized bias is informative. If positive, it signifies that treated youth (i.e., youth who work intensively during the school year) exhibit more of the characteristic being measured than untreated youth. Conversely, if negative, it means that treated youth have less of the measured quality than untreated youth.

- 17.
If a logistic regression model of substance use is estimated instead, the coefficient for intensive work with no control variables is 0.77 (odds ratio = 2.16), and with control variables is 0.28 (odds ratio = 1.33). Both coefficients are statistically significant at a five-percent level.

- 18.
Notice that the ATE from standard regression in panel A (

*b*=0.051) is very similar to the ATE from propensity score regression with no trimming in panel B (*b*=0.054). The similarity is not coincidental. The discrepancy is only due to the fact that the propensity score was estimated from a logistic regression model at the first stage. Had a linear regression model been used instead, the two coefficients would be identical, although the standard errors would differ. - 19.
We employ the user-written Stata protocol -psmatch2- to estimate average treatment effects from the matching models (see Leuven and Barbara 2003). To obtain the standard error of the ATE, we perform a bootstrap procedure with 100 replications.

- 20.
As a further test of sensitivity, we estimated the ATE of intensive employment on substance use for subsamples with different substance use histories. For this test, we employed single-nearest-neighbor matching with no caliper, although the findings were not sensitive to this choice. Among the 2,740 youth who, at the initial interview, reported never having used illicit substances, ATE=0.084 (S.E.=0.060). Among the 1,927 youth who reported having used at least one type of illicit substance prior to the initial interview, ATE=−0.019 (S.E.=0.046).

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Apel, R.J., Sweeten, G. (2010). Propensity Score Matching in Criminology and Criminal Justice. In: Piquero, A., Weisburd, D. (eds) Handbook of Quantitative Criminology. Springer, New York, NY. https://doi.org/10.1007/978-0-387-77650-7_26

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