Difference between revisions of "Quasi-Experimental Methods"
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== Guidelines == | == Guidelines == | ||
=== The Power of Quasi-Experimental Methods === | === The Power of Quasi-Experimental Methods === | ||
Like experimental methods, quasi-experimental methods aim to solve the problems of [[confoundedness]] and [[reverse or simultaneous | Like experimental methods, quasi-experimental methods aim to solve the problems of [[Unconfoundedness Assumption | confoundedness]] and [[Exogeneity Assumption# Reverse Causality Bias | reverse]] or [[[[Exogeneity Assumption#Simultaneity Bias | simultaneous]] causality in identifying the marginal effect of a change in condition. Unlike [[Experimental Methods | experimental methods]], quasi-experiments tend to be based on policy changes or natural events that were not actually randomly assigned, but occurred in such a way that they can be considered "[[as good as randomly assigned]]" relative to some of the outcomes under consideration. Two examples illustrate these differences well. | ||
First, consider a time-based shock that can potentially apply to all people participating in a given market, such as joining a job guarantee program. [[Regression Discontinuity]] and [[Event Study]] designs are natural choices in such a situation, but comparing across time (ie, before and after the join date) at the individual level is inappropriate, since individuals may have joined the program due to other factors that would have affected their income, such as job market seasonality, business failure, or family changes. This type of [[reverse causality]] confounds the effect of the estimate because the true [[counterfactual]] cannot be estimated. | First, consider a time-based shock that can potentially apply to all people participating in a given market, such as joining a job guarantee program. [[Regression Discontinuity]] and [[Event Study]] designs are natural choices in such a situation, but comparing across time (ie, before and after the join date) at the individual level is inappropriate, since individuals may have joined the program due to other factors that would have affected their income, such as job market seasonality, business failure, or family changes. This type of [[Exogeneity Assumption# Reverse Causality Bias | reverse causality]] confounds the effect of the estimate because the true [[counterfactual]] cannot be estimated. | ||
Instead, it is necessary to use a population-level cutoff such as the implementation of the program in an area [[differences-in-differences]] or [[staged rollout]] designs, or, if only one area is implementing the policy, [[Synthetic Control Method | synthetic control]] methods or the assumption that events occurring on either side of the policy cutoff could not manipulate on which side of the cutoff they occurred (the [[running variable]]). | Instead, it is necessary to use a population-level cutoff such as the implementation of the program in an area [[Difference-in-Differences | differences-in-differences]] or [[staged rollout]] designs, or, if only one area is implementing the policy, [[Synthetic Control Method | synthetic control]] methods or the assumption that events occurring on either side of the policy cutoff could not manipulate on which side of the cutoff they occurred (the [[running variable]]). | ||
Second, consider a natural disaster that has a various impact across space, such as an earthquake with a random fault/epicenter activation. Assuming that there was no way for households to foresee the timing or location of the earthquake, and that there was no serious [[differential attrition]] on critical dimensions, it can be used as a natural experiment on outcomes later in life for affected individuals. However, for the input component to be truly [[exogenous]], something like the distance to the faultline should be used as the treatment variable - even though estimates of local magnitude may be available. | Second, consider a natural disaster that has a various impact across space, such as an earthquake with a random fault/epicenter activation. Assuming that there was no way for households to foresee the timing or location of the earthquake, and that there was no serious [[differential attrition]] on critical dimensions, it can be used as a natural experiment on outcomes later in life for affected individuals. However, for the input component to be truly [[Exogeneity Assumption | exogenous]], something like the distance to the faultline should be used as the treatment variable - even though estimates of local magnitude may be available. | ||
This is because the local magnitude may be correlated with other varying characteristics (such as soil quality or hilliness) that also contribute to the outcomes (such as family income) and therefore re-introduce the confounding problem by including a non-random component that is correlated to a key characteristic. Distance from a randomly placed disaster, though a less precise measure of "exposure", is critically uncorrelated with almost any imaginable outcome under the correct assumption (unlike, for example, distance to a volcano, or to a tsunami-affected shoreline). | This is because the local magnitude may be correlated with other varying characteristics (such as soil quality or hilliness) that also contribute to the outcomes (such as family income) and therefore re-introduce the confounding problem by including a non-random component that is correlated to a key characteristic. Distance from a randomly placed disaster, though a less precise measure of "exposure", is critically uncorrelated with almost any imaginable outcome under the correct assumption (unlike, for example, distance to a volcano, or to a tsunami-affected shoreline). | ||
== Additional Resources == | == Additional Resources == | ||
Revision as of 23:19, 9 February 2018
Impact evaluations aim to identify the impact of a particular intervention or program (a "treatment"), by comparing treated units (households, groups, villages, schools, firms, etc) to control units. Well-designed impact evaluations estimate the impact that can be 'causally attributed' to the treatment, i.e. the impact that was a result of the treatment itself not other factors. The main challenge in designing a rigorous impact evaluation is identifying a control group that is comparable to the treatment group. The gold-standard method for assigning treatment and control is randomization. In cases where randomization is not possible, quasi-experimental methods can be used. To design a rigorous impact evaluation, it is essential to have a clear understanding of the Theory of Change.
Introduction
Unlike in experimental research methods, the investigator does not have direct control over the exposure. "Natural experiments", such as regression discontinuity designs and event studies, identify existing circumstances where assignment of treatment has an exploitable element of randomness. In other cases, researchers attempt to simulate an experimental counterfactual by constructing a control group that is as similar as possible to the treatment group, using techniques such as propensity score matching.
Guidelines
The Power of Quasi-Experimental Methods
Like experimental methods, quasi-experimental methods aim to solve the problems of confoundedness and reverse or [[ simultaneous causality in identifying the marginal effect of a change in condition. Unlike experimental methods, quasi-experiments tend to be based on policy changes or natural events that were not actually randomly assigned, but occurred in such a way that they can be considered "as good as randomly assigned" relative to some of the outcomes under consideration. Two examples illustrate these differences well.
First, consider a time-based shock that can potentially apply to all people participating in a given market, such as joining a job guarantee program. Regression Discontinuity and Event Study designs are natural choices in such a situation, but comparing across time (ie, before and after the join date) at the individual level is inappropriate, since individuals may have joined the program due to other factors that would have affected their income, such as job market seasonality, business failure, or family changes. This type of reverse causality confounds the effect of the estimate because the true counterfactual cannot be estimated.
Instead, it is necessary to use a population-level cutoff such as the implementation of the program in an area differences-in-differences or staged rollout designs, or, if only one area is implementing the policy, synthetic control methods or the assumption that events occurring on either side of the policy cutoff could not manipulate on which side of the cutoff they occurred (the running variable).
Second, consider a natural disaster that has a various impact across space, such as an earthquake with a random fault/epicenter activation. Assuming that there was no way for households to foresee the timing or location of the earthquake, and that there was no serious differential attrition on critical dimensions, it can be used as a natural experiment on outcomes later in life for affected individuals. However, for the input component to be truly exogenous, something like the distance to the faultline should be used as the treatment variable - even though estimates of local magnitude may be available.
This is because the local magnitude may be correlated with other varying characteristics (such as soil quality or hilliness) that also contribute to the outcomes (such as family income) and therefore re-introduce the confounding problem by including a non-random component that is correlated to a key characteristic. Distance from a randomly placed disaster, though a less precise measure of "exposure", is critically uncorrelated with almost any imaginable outcome under the correct assumption (unlike, for example, distance to a volcano, or to a tsunami-affected shoreline).
Additional Resources
- list here other articles related to this topic, with a brief description and link