The net effects of medical malpractice tort reform on health insurance losses: the Texas experience

Reasons for the disagreement in the literature could arise from a number of sources including differences in sample characteristics, time periods, or econometric methods. As such, the additional evidence on the influence of malpractice exposure on the frequency/cost of services rendered by medical providers, presented in our analysis, is a valuable contribution to the ongoing debate in the literature.

For example, using data from the Physician Insurance Association of America (PIAA), Kessler and McClellan [24] find evidence that direct malpractice reforms reduce defensive medicine practices but do not influence health outcomes. Baicker, Fisher, and Chandra [25] find a positive relation between Medicare spending, especially on imaging services, and malpractice awards which provides support for the hypothesis that malpractice awards drive defensive medicine rates.

For example, Mello et al. [26] provide evidence that suggests physicians reduce or eliminated “high risk” aspects of their practice. Kessler, Sage, and Becker [27] provide evidence that tort reforms increase the supply of physicians.

This is not a universal sentiment in the literature. For example, Morrisey, Kligore, and Nelson [4] do not find any evidence that damage caps reduce the cost of employer sponsored health insurance. Given somewhat conflicting results in prior literature, our analysis is valuable in that it provides insight into the ongoing debate regarding how the medical professional liability climate ultimately influences the health insurance market.

In 2008 ten plaintiffs filed a federal lawsuit claiming the state’s non-economic cap violates the U.S. Constitution. The suit, similar to those filed in other states with such caps, argued that the cap has a direct impact on an injured patient’s potential jury award and, consequently, influences the value of filing the suit in the first place. A federal judge ruled that the cap was constitutional in 2012.

Interestingly, Hyman et al. [28] evaluate physician supply in Texas before and after the 2003 reforms. They find that physician supply in Texas was not deteriorating before 2003 and “did not measurably improve after the reform” (p.203).

Other Texas-specific studies include Friedson and Kniesner [29], who examine how the reform – specifically the non-economic damages cap – has affected pre-trial settlement speed and settlement amounts. They find that even though injured plaintiffs are compensated more quickly after reform, they receive a lower settlement. In addition, Paik, Black, Hyman, Sage, and Silver [20] evaluate the influence of the Texas reform on elderly patients. They find that tort reform strongly affected claim rates and payouts for all patients, but elderly claimants receive disproportionately lower payouts after reform. Further, a recent review of the Texas market indicates, among other things, that “the reform bill’s most significant achievements have been increased access to health care and an unanticipated positive economic impact on the Texas economy. By the end of 2013, 10 years and three months after the effective date of HB4, the number of licensed physicians in the state will almost have doubled” [19].

Paik et al. [22] posit a similar hypothesis regarding physicians’ perception of malpractice risk.

While much of our analysis relies on the NAIC’s health insurance database, we also utilize the property-casualty database for private passenger automobile loss data. Both databases also contain information relating to overall company financial information (for example, assets, liabilities, organizational form). However, the analysis presented here relies strictly on data from the state pages.

The dataset includes financial data filed with state insurance departments for all insurers classified as health insurers and much of the data, including premiums, claims, and enrollment, are reported separately for each state in which an insurer operates

Specifically, we restrict our sample to firms with at least $100,000 in direct premiums written, $100,000 in direct losses incurred, and 1000 enrollees. The inclusion of these filters does not substantially reduce our sample size and helps to reduce the effects of outliers in our analysis. These filters ensure that the insurers included in our analysis are non-trivial market participants in a given state that are likely to be influenced by the operational and regulatory climate of a given state.

This filter effectively ensures that we analyze firms that were operating before and after the Texas reform took effect.

Previous studies similar in nature to ours (for example, [22]) evaluate relative spending levels scaled by enrollees. In addition, because the size of health insurance markets, in terms of premium levels and insurers vary widely across states, it would be inappropriate to evaluate raw, unscaled loss levels across states. Further, a loss measure scaled by premiums is more indicative of financial/operational performance of the health insurer while losses scaled by plan participants (enrollees) better quantifies the amount of claims that insurance companies incur due to patients’ interactions with medical providers. We therefore believe that scaling by enrollees is the most appropriate method for our analysis.

The NAIC Health Insurance database, due to changes in reporting requirements, does not provide consistent and reliable data that can be used in our study before 2001. As such, we are forced to limit the start of our sample to 2001.

Such DD analyses are frequently used in the economics, finance, and insurance literature (for example, [22, 30, 31]). The method involves computing the difference between the pre- and post-, within-subjects differences of the treatment and control groups. As it applies to our analysis, the subjects are a sample of health insurance companies, the treatment group is a sub-sample of health insurers operating in Texas, and the non-treated group is a sub-sample of health insurers operating in other states.

Health insurers operating in Florida, Georgia, Illinois, Mississippi, Nevada, Ohio, Oklahoma, Oregon, and South Carolina are not included in this subsample.

These 18 states are Alabama, Arizona, Arkansas, Connecticut, Delaware, Iowa, Kentucky, Maine, Minnesota, New Hampshire, New York, North Carolina, Pennsylvania, Rhode Island, Tennessee, Vermont, Washington, and Wyoming. Paik et al. [22] also include the District of Columbia but, due to the unavailability of certain demographic data, we are forced to omit insurers operating there in our analysis.

These 9 states are Alabama, Arizona, Arkansas, Iowa, Kentucky, Minnesota, Tennessee, Washington, and Wyoming.

We recognize that some of the states in these subsamples enacted other reforms relating to medical malpractice during our sample period but, following Paik et al. [22], we believe these other reforms are not likely to cause major changes in losses per enrollee and are confident in the validity of these samples.

Studies such as Bertrand, Duflo, and Mallainthan [32] and Donald and Lang [33] suggest that, in certain cases, econometric issues lead researchers to incorrectly reject the null hypothesis of the statistical significance of a difference-in-differences coefficient. These studies provide evidence that clustering standard errors helps reduce the likelihood of a false rejection of the null. All results reported throughout the paper are from models with standard errors clustered at the firm level. In unreported results, we also implement another procedure found by Bertrand et al. [32] to reduce the likelihood of an inaccurate rejection of the null, the block bootstrap procedure. Our main results remain unchanged when the block bootstrap procedure is implemented. Further, our main results remain unchanged when we cluster standard errors by state and also when we include state and year effects (instead of the Treat and Reform dummies in the main specification). Therefore, we do not believe that the common econometric pitfalls of DD analysis described in the literature bias our results.

For example, changes in the number of people with health insurance.

We select private passenger automobile physical damage insurers because this line of business strictly relates to property losses. As such, factors associated directly with medical malpractice tort reform (for example, liability lawsuits, physician behavior, and the like) do not influence loss levels in this line of business. Similarly, factors associated directly with health insurance (doctors, healthcare costs, and so on) also do not influence loss levels in this line of business. Thus loss levels in private passenger automobile physical damage insurance are an appropriate control.

Note the “DD Estimator” coefficients and statistical significances reported are the regression coefficients of Treat ^∗ Reform from equation 1. However, in this output, Reform takes the value of 0 if the year is 2002 and 1 if the year is either 2004, 2005, 2006, 2007, 2008, 2009, or 2010, depending on the specification.

These results are available from the authors upon request.

For the same reasons described in a previous footnote, all reported results are from models with standard errors clustered at the firm level. In addition, all reported results are robust to different clustering strategies described in a previous footnote as well as various combinations of state-level control variables.

These are the same control variables included in the DD analysis which are defined in a previous footnote. In addition, unreported analysis indicates that our main result is robust to the inclusion of additional/alternative demographic controls, such as uninsured rates and educational attainment.

Note the “DDD” estimates and statistical significances reported in the table are the regression coefficients of Treat*Control*Reform from equation 2. However, in this output, Reform takes the value of 0 if the year is 2002 and 1 if the year is either 2004, 2005, 2006, 2007, 2008, 2009, or 2010, depending on the specification.