Longitudinal Propensity Score Matching: A Demonstration of Counterfactual Conditions Adjusted for Longitudinal Clustering

Abstract

Objectives

Given the challenges of conducting experimental studies in criminology and criminal justice, propensity score matching (PSM) represents one of the most commonly used techniques for evaluating the efficacy of treatment conditions on future behavior. Nevertheless, current iterations of PSM fail to adjust for the effects of longitudinal clustering on participant exposure to treatment conditions. The current study presents and evaluates longitudinal PSM (LPSM) as an alternative method for assessing the effects of a treatment condition on future behavior. LPSM adjusts for the effects of longitudinal clustering (i.e., clustered error) by assuming that the association between a cross-sectional predictor and a treatment condition varies depending upon the time at which the treatment was administered.

Methods

Two general steps were taken to evaluate the validity of LPSM. First, we conducted a series of simulation analyses to illustrate the LPSM method. Second, we further demonstrate the method using data from 63,899 inmates incarcerated in Ohio prisons by assessing the effects of prison programming on recidivism over a three-year post-release period. Disparities in treatment effects were compared between cross-sectional PSM and LPSM.

Results

The simulation and demonstration analyses produced evidence of disparities in results between LPSM and cross-sectional PSM. LPSM appeared to provide the superior adjustment for longitudinal clustering relative to cross-sectional PSM.

Conclusions

LPSM provides a useful alternative to cross-sectional PSM when the probability of exposure to a treatment condition varies by the time at which the treatment was administered.

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Fig. 1
Fig. 2

Notes

  1. 1.

    While longitudinal analyses have certainly advanced criminological research, recently scholars have noted that an over-reliance on longitudinal modeling and an accompanying disregard for cross-sectional research could have a range of negative consequences (see Cullen et al. 2019).

  2. 2.

    Longitudinal models adjust for longitudinal clustering of data at observation time points, while generalized hierarchical linear modeling adjusts for macro-level clustering at units of analysis larger than the individual.

  3. 3.

    It is not, however, required for the unspecified aggregate treatment condition to be transformed into a dichotomous construct since propensity score estimation techniques exist for ordinal and continuous constructs (Guo and Fraser 2014).

  4. 4.

    The logic for averaging comes from the mathematical process underlying the estimation of coefficients in a growth curve longitudinal model. Specifically, while a single coefficient is produced for the interaction between a time invariant variable and time on a time variant dependent variable, the coefficient is a time weighted effect based on the trend (Fitzmaurice et al. 2008). Explicitly, the interaction between time and a time invariant variable represents the average effects on the trend (Fitzmaurice et al. 2008). The use of average time sensitive predicted probabilities is just one possible method. As outlined by Guo and Fraser (2014), there are a host of techniques that can be used to approximate a quasi-experimental design with propensity scores. For example, Mahalanobis distance matching, propensity score weighting, optimal matching, and a highly saturated group-based trajectory analysis represent a few of the potential techniques. Each of the techniques described above, however, would have to be adapted to a longitudinal application. As such, for the sake of parsimony, we focus on nearest neighbor matching.

  5. 5.

    The associations in the simulated dataset were specified as linear and all of the variables were specified to be normally distributed. As such, we did not need to test the assumptions because the simulated dataset was specifically created to satisfy these assumptions.

  6. 6.

    We encourage the replications to specify different scenarios in order to observe differences in bias across scenarios.

  7. 7.

    To ease comparisons between the methodologies, percent bias was evaluated in a three category sub-classification: substantive, noticeable, and minor (Apel and Sweeten 2010; Guo and Fraser 2014). Substantive biases were classified as percent biases greater than 15%, which are likely indicative of failure to achieve common support between the treatment and control cases. Noticeable biases were classified as percent biases greater than 5% and less than 15%. Deviations within this range commonly indicate noticeable differences in the distribution of the specified covariate between the treatment and control cases. Minor biases were characterized as percent biases less than 5%. These values are reasonably influenced by the sample size and are feasibly indicative of minor variation in the distribution of the specified covariate between the treatment and control cases.

  8. 8.

    The Evaluation of Ohio’s Prison Programs was a retrospective study of programing amongst 88,621 unique inmates (105,945 cases with 16 percent reflecting inmates who served multiple sentences during the study period) incarcerated in the Ohio Department of Rehabilitation and Correction (ODRC) between January 2008 and June 2012. For more information on the study, see Latessa et al. (2015), Lugo et al. (2017), and Pompoco et al. (2017). Due to the three-year follow up period for recidivism, only inmates released prior to January of 2012 were included within the analytical sample. In total, 63,899 inmates were included in the analytical sample.

  9. 9.

    Due to the unbalanced nature of the longitudinal data, a three-year period was selected because the number of individuals incarcerated and participating in treatment programming 3 years after their admission is extremely limited.

  10. 10.

    Three-month periods were selected to ensure that limited overlap in programming exposure existed between the months from admission blocks (MFABs).

  11. 11.

    Due to data limitations, the completed/termination date for non-reentry approved programs was not recorded. Furthermore, the length of the non-reentry approved programs was not recorded. As such, the exposure to programming at each MFAB represents the MFAB in which we are certain that an inmate received programming.

  12. 12.

    \(\bar{X}\) = 229.31 and SD 12.21. Following the guidance of prior scholarship (e.g., Silver and Nedelec 2018) the natural standard deviation was selected as the cut point because the scores on the CASAS exam were normally distributed.

  13. 13.

    As a sensitivity analysis, the entire analytical process was replicated using nearest neighbor matching with a caliper of .05. The results of these analyses are presented in Online Appendix D. As illustrated in Online Appendix D, the overall results were similar when using the different calipers.

  14. 14.

    The results of this supplemental analysis can be provided upon request.

  15. 15.

    As a reminder, the simulation analyses used a caliper of .05 while the demonstration with real data used a caliper of .001.

  16. 16.

    Both estimates are biased because a large portion of the variation in the longitudinal treatment variables was specified to be associated with a unique normally distributed random variable. These unique normally distributed random variables were used to create the longitudinal clustering in the simulated dataset. This specification allows us to observe that the RIS estimates are closer to the true estimates than the BLR estimates but is reliant on random variables. Simply, because a large portion of the variation in the longitudinal variables are attributed to unique random variables, the estimates and matching procedures are unable to capture variation associated with these measures, which in turn makes both sets of estimates biased. To reduce the bias in both estimates, you can reduce the amount of variation the normally distributed random variables contribute to each time period in the simulation. This, however, could create a scenario where it would difficult to discern which method is significantly closer to the point estimate. Additionally, we could have created a simulated dataset where the clustering variables were correlated with the constructs used to match participants (x1–x5), representing an unobserved time variant predictor of exposure to the treatment. This specification, however, requires the user to properly know how to structure clustering variables and specify correlation between observed and unobserved constructs. The coding specifications in R are substantively more difficult to edit and understand. Considering this, we wanted to provide the reader with R-code that can be easily adapted by a non-frequent user of R.

  17. 17.

    The data represent an unbalanced, rather than censored, data design. In the current context, the unbalanced design is characterized by the knowledge that after an inmate’s release from prison it is not possible to participate in inmate programs. While this might be a concern, scholars have addressed this issue and demonstrated robust findings can be observed when employing an unbalanced data design (e.g., Diggle and Kenward 1994; Fitzmaurice et al. 2011). The decline in program participation throughout the 12 MFABs likely corresponds to two factors. First, the program participation amongst motivated inmates is likely to reduce as a result of the inability to restart an already completed program. Generally, only a limited number of programs are offered at each facility and it is likely that motivated inmates complete the majority of programs available at their facility. Second, the reductions in program participation could correspond to the early release of more prosocial inmates.

  18. 18.

    The model results and weighting estimates for the ten covariates for the BLR and RIS models (respectively) are presented in Table H1 and Table H2 of Online Appendix H.

  19. 19.

    As observed in Figure C1 in the Online Appendix, the median propensity score estimated with the RIS model is likely attenuated by the predicted probabilities estimated for the last three MFABS.

  20. 20.

    Briefly, LPSM represents one method of employing longitudinal propensity scores to approximate the counterfactual condition. Alternative methods such as, Mahalanobis distance matching, propensity score weighting, optimal matching, and a highly saturated group-based trajectory analysis could be adapted to approximate a counterfactual condition using longitudinal propensity scores.

  21. 21.

    The two demonstrations provided in the main text were replicated using the random intercept model and random slope model. The results of these demonstrations can be provided upon request.

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Silver, I.A., Wooldredge, J., Sullivan, C.J. et al. Longitudinal Propensity Score Matching: A Demonstration of Counterfactual Conditions Adjusted for Longitudinal Clustering. J Quant Criminol 37, 267–301 (2021). https://doi.org/10.1007/s10940-020-09455-9

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Keywords

  • Longitudinal propensity score matching
  • Longitudinal data
  • Longitudinal clustering
  • Evaluation of programs