The Repeal of Noneconomic Damage Caps and Medical Malpractice Insurance Premiums

Abstract

Noneconomic damage caps are controversial because they seek to balance uncertain benefits through reductions in physician precautionary costs, against uncertain harms to patient welfare. Opposing policy actions at the state-level reflect this controversy as some states have enacted noneconomic damage caps over the past few decades while others repealed their caps. Our difference-in-differences analyses suggest that repeals increase premiums. These increases are larger after State Supreme Court decisions, affecting all cases in a state, compared with State Circuit Court decisions affecting only specific cases. Magnitudes differ by physician specialty, with larger effects observed in obstetrics/gynecology and general surgery, compared with internal medicine. Our estimates of these repeals are larger than estimates on enactments reported in the literature, suggesting a potential asymmetry between enacting and repealing damage caps.

I. Introduction

The economic theory of tort law is based on the idea that an optimal level of liability for injury should be chosen, such that total societal costs are minimized, including harm suffered by victims, the cost of precaution, and administrative costs of litigation (Miceli, 2009). This optimal level of liability varies depending on the context and should be determined by comparing the costs of harm against the cost of taking precautions. In the context of medical malpractice, the societal and economic costs of patient harm can be substantial. However, unlike other settings, the cost of precaution can also be extraordinarily high in healthcare (Frakes & Gruber, 2019). To avoid liability, physicians may practice defensive medicine and purchase excess malpractice insurance coverage. These increases in precaution costs might not be borne solely by physicians, but also passed on to patients in the form of higher medical care expenditures and potential harms to health from overtreatment. Thus, identifying an optimal level of liability is particularly challenging and controversial in medical settings.

This challenge and controversy can be illustrated by a specific form of tort reform in healthcare – noneconomic damage caps, which place a limit on the monetary amount that patients can be awarded for noneconomic damages caused by physician negligence. Noneconomic damages encompass a wide range of damages, including emotional distress, physical pain and suffering, permanent disfigurement, or loss of enjoyment of life. While noneconomic damage caps intend to reduce physicians’ exposure to liability stemming from negligence, such caps are associated with both benefits and potential unintended negative consequences for patient welfare. Providing physician protection from liability may help decrease the costs associated with defensive medicine and increase physician supply (Agarwal et al., 2019). At the same time, these protections afforded to physicians may increase physicians’ propensity to partake in risky or negligent medical practices, resulting in lower patient welfare and higher societal costs (Bertoli & Grembi, 2019; Currie & MacLeod, 2008; Dubay et al., 2001; Yang et al., 2009). Noneconomic damage caps have thus been a source of contention in the United States.

Contrasting policy actions across states over the past decade have reflected this controversy about noneconomic damage caps. While some states (e.g., North Carolina) introduced such caps, others (e.g., Georgia and Illinois) decided to repeal their pre-existing caps. Prior research has examined the impacts of introducing these noneconomic damage caps on various study outcomes, such as health care quality and costs, private health insurance market, provider reimbursement, and medical malpractice insurance premiums (Avraham & Schanzenbach, 2015; Born et al., 2017; Frakes & Jena, 2016; Friedson, 2017; Kessler & McClellan, 2002; Kilgore et al., 2006; Yu et al., 2017; Yu & Baker, 2022). However, few studies have assessed the effects of repealing these caps, with the exception of two papers that examined changes in physician provision of medical services and procedures (Dy et al., 2020; Mushinski et al., 2022). To the best of our knowledge, this study is one of the first to evaluate how repealing noneconomic damage caps affects medical malpractice insurance premiums, a measure of physician liability risk.

We believe this to be an important outcome to study for several reasons. First, medical tort reforms, such as noneconomic damage caps, intend to reduce physician liability risk; given prior study findings that noneconomic damage caps reduced the liability risk as measured by medical malpractice insurance premiums (Yu & Baker, 2022), we hypothesize that repealing such caps may increase the premiums for physicians. Our study aims to test this hypothesis and offer a first look at these repeals from the lens of physician malpractice insurance premiums, which will complement the few published studies that assessed the repeals’ effects on patients’ healthcare (Dy et al., 2020; Mushinski et al., 2022). Second, in contrast to introducing a noneconomic damage cap, the repeal of such a cap may induce stronger behavioral responses by physicians given their risk averse preferences as identified by prior studies (Arrieta et al., 2017; Galizzi et al., 2016; Ruggeri & van der Pol, 2012). Such asymmetric responses by physicians are important to consider for policymakers contemplating medical tort reform.

We first present a conceptual framework that hypothesizes the potential effects of repealing noneconomic damage caps on medical malpractice insurance premiums. Our framework suggests that repealing noneconomic damage caps may increase the size of a potential loss for both malpractice insurance firms and physicians and subsequently lead to higher medical malpractice insurance premiums. Higher premiums can be driven by a supply-side price increase and/or an increase in demand for premiums by physicians.

To empirically test these predictions, we examine court rulings where noneconomic damage caps were deemed unconstitutional in the Database of State Tort Law Reforms (7^th edition) (Avraham, 2021), and focus our attention on two states– Georgia and Illinois, both of which meet our selection criteria as discussed below. We apply a difference-in-differences (DD) framework to understand the impacts of the repeals on medical malpractice insurance premiums during the study period between 2005 and 2019. Because we are interested in the repeals’ effects, our counterfactual of interest is states that still have noneconomic damage caps in place during our study period. We thus compare county-level premiums between states that repealed their noneconomic damage cap to states that retained their noneconomic damage caps, before and after repeals occurred. We further examine the sensitivity of our choice of control group by including only control states that are within the same region as a treated state.

We find that the repeal of noneconomic damage caps increases average premiums, beginning after State Circuit Court decisions and growing further following State Supreme Court decisions. Our study is thus one of the first to separate the effects of State Circuit Court decisions, which are effective only for specific cases, from that of State Supreme Court decisions, which are effective for all cases in a state. While the increases in premiums are similar between Georgia and Illinois, we find heterogeneous effects by physician specialty with premiums increasing more in high-risk specialties, such as obstetrics/gynecology and general surgery, compared to that of internal medicine. Though noisily estimated in some specifications, the estimated effect sizes are larger compared to the effect sizes reported in prior literature on the introduction of a noneconomic damage cap, pointing to the possibility of asymmetric effects between enacting and repealing noneconomic damage caps.

Our results contribute not only to the intersection of law and health economics, but also more broadly to the literature on behavioral economics. Loss aversion in prospect theory posits that individuals respond more strongly to the possibility of losses compared to equivalent gains, while risk aversion posits that certain individuals prefer certainty over uncertainty (Kahneman & Tversky, 1979). Our findings are broadly consistent with the notion that physicians may exhibit loss- and risk-averse preferences (Arrieta et al., 2017; Galizzi et al., 2016; Ruggeri & van der Pol, 2012). This has ramifications for tort law, as the cost of higher exposure to liability might be understated in current legal and healthcare debates.

The rest of the paper is organized as follows. In Section II, we describe our conceptual framework for understanding the potential mechanisms by which the repeal of a noneconomic damage cap affects malpractice insurance premiums. In Section III, we outline the data and methods. Section IV discusses the results, and Section V concludes the study with some policy implications and directions for future research.

II. Conceptual Framework

Repealing noneconomic damage caps can affect medical malpractice insurance premiums through a variety of mechanisms. In competitive insurance markets with actuarially fair pricing, physicians may fully insure against malpractice risk by purchasing coverage equal to their expected financial loss in the event of a payout. When a noneconomic damage cap is repealed, the potential size of a malpractice award increases, which raises the expected loss associated with a lawsuit. In response, physicians may choose to purchase higher coverage limits to maintain financial protection. Additionally, physicians may perceive the probability of being sued to be higher after repeals, as larger potential payouts could make lawsuits more attractive to plaintiffs and attorneys. The combined effect of a larger expected loss and greater perceived litigation risk can thus increase the demand for malpractice insurance coverage among physicians; this increase in demand may subsequently contribute to rising premiums.

At the same time, insurance companies may independently raise prices in response to this heightened risk environment introduced by cap repeals. If repeals increase the probability of a payout, then the price per unit of coverage will increase for insurers to remain profitable. As a result, both the demand for malpractice insurance coverage and the price of that coverage may rise following the repeal of a noneconomic damage cap, leading to observable increases in average malpractice insurance premiums.¹ Our empirical analysis below quantifies these effects.

III. Data and Methods

A. Study Sample

Selection Criteria for the Treated States

We began by identifying all states that were coded as repealing their noneconomic damage caps between 2005 to 2019 in the Database of State Tort Law Reforms (7^th edition) (Avraham, 2021). Among the seven states identified (Georgia, Illinois, Missouri, Mississippi, Utah, Kansas, and Florida), we focus our attention on two for this study – Georgia and Illinois, as both states meet the following selection criteria. First, these repeals were fully binding as State Supreme Court decisions in both states, affecting all cases in each state, unlike lower court decisions that affect only specific cases in a state. Second, the caps that were repealed in Georgia and Illinois were for noneconomic damages stemming from medical liability broadly, unlike some states that repealed their caps only for specific liabilities such as wrongful deaths. For the three states (Missouri, Mississippi, and Utah) that were coded as repealing their caps in the database but did not meet the above criteria, we consider them as partial, incomplete, or confounded repeals and provide an analysis of them in the Online Appendix Section A. We expect these types of repeals to have no effect on premiums because they were limited in scope or non-binding. Finally, Kansas and Florida were omitted from the study because these states repealed their noneconomic damage caps at the end of the study period in 2019 and 2017. Florida also introduced a sovereign immunity recovery cap in 2011 persisting until the end of the study period, further complicating estimation. Our discussion below focuses on Georgia and Illinois.

Georgia

In 2005, Georgia introduced a cap of $350,000 on noneconomic damages stemming from medical malpractice, including wrongful deaths (Ga. Code Ann. § 51–13-1). In February 2009, the Georgia trial court found this cap unconstitutional, and subsequently entered judgement in the full amount of $1,265,000. After the defendant, Oculus, appealed, the Georgia Supreme Court affirmed the trial court’s ruling on March 22, 2010 that the noneconomic damage cap was unconstitutional (Atlanta Oculoplastic Surgery, P.C. v. Nestlehutt, 691 S.E.2d 218 (Ga. 3/22/2010).² Although decisions in the trial court are not binding in Georgia, there may have been anticipatory effects of an affirmation by the Supreme Court of the trial court ruling. Thus, we consider 2005–2008 as the pre-treatment periods for Georgia, and 2009–2019 as the post period. The post period includes two parts—(1) between the circuit court decision in 2009 and the Georgia supreme court decision in 2010, and (2) after the Georgia Supreme Court decision in 2010; we assess whether the treatment effect differs between the two periods. We also conduct a sensitivity check by dropping 2009 from our analysis since the decision in that year by the trial court was not binding until confirmed by the state’s Supreme Court in 2010.

Illinois

In 2005, Illinois introduced a cap of $1,000,000 on noneconomic damages stemming from medical malpractice for hospitals and a $500,000 cap for physicians and/or their business. This cap was ruled unconstitutional by the Illinois Circuit Court on November 13, 2007, and by the State Supreme Court on February 4, 2010 (Lebron v. Gottlieb Mem’l Hosp., 930 N.E.2d 895 (Ill. 2/4/2010).³ Circuit court decisions may set a precedent for future decisions within the same district in Illinois but are non-binding for other court districts in the same state. Thus, we consider the possibility of anticipatory effects of an affirmation by the State Supreme Court of the circuit court ruling. Given that the circuit court decision was at the very end of 2007 (mid-November), we consider 2005–2007 as the pre-treatment period for Illinois, and 2008–2019 as the post period. We examine whether the treatment effect differs between two parts of the post-treatment period— (1) 2008–2009, i.e., between the circuit court decision and before the State Supreme Court decision, and (2) 2010–2019, i.e., after the State Supreme Court decision. We also conduct a sensitivity check by dropping 2008–2009 from our analysis since the Circuit Court decision in 2008 was not binding until confirmed by the state’s Supreme Court in 2010.

We analyze Georgia and Illinois separately for a few reasons. First, the period between each state’s circuit court decision and Supreme Court decision differs; thus, it would be impractical to overlay them in an event study if we are interested in both the interim and enforcement effects of repeals. Second, while these two laws are largely similar, they still hold a few differences. For instance, the cap for individual businesses in Georgia was $350,000, compared with $500,000 in Illinois.

Counterfactual States

Given that our treatment of interest is the removal of noneconomic damage caps, our control group of interest are states that are still capped for the entire study period from 2005 to 2019. We identified 18 such control states from the Database of State Tort Law Reforms (7^th edition) and listed them in Table B1 in the Online Appendix. We drop California because it introduced a split recovery reform, which apportions punitive damages between the state and the plaintiff to mitigate financial incentives for plaintiff attorneys to pursue punitive damages, during our study period, Massachusetts because of Romney Care, and Florida because it was treated near the end of the study period and introduced additional reforms during the study period, leaving 15 control states in our final analytic sample. The key assumption in a potential outcome framework is that the trends in premiums for states that repealed their noneconomic damage caps would have been the same as the states that still have their caps in place, had the treatment states not repealed their caps. We believe this to be a reasonable assumption when using the still capped states as our counterfactual as opposed to, say, those states that never adopted noneconomic damage caps. We first note that when one uses never capped states as a control group, there is remarkable evidence of non-parallel trends in the pre-period for both states, but particularly for Illinois (Figure B3). Second, conceptually, one may consider how premiums in states with noneconomic damage caps may respond differentially to unobservable shocks compared to states that do not have noneconomic damage caps. If premiums respond differentially to aggregate shocks depending on whether noneconomic damage caps are in place, then still capped states serve as our best approximate counterfactual. Third, never capped states are “always treated” in our study and are thus omitted from the main analysis but included as a robustness check in the Appendix. While one cannot directly observe whether common shocks and parallel trends assumptions are satisfied into the post-period, for the above reasons, we utilize still capped states as the control group.

B. Medical Malpractice Premiums

We use data on medical malpractice insurance premiums from the Medical Liability Monitor (MLM) for the years between 2005 and 2019. The MLM data cover three medical specialties—general surgery, obstetrics/gynecology (OB-GYN), and internal medicine—allowing us to assess the possibility of heterogeneous treatment effects across specialties. Of these three specialties, general surgery and OB-GYN are considered specialties with high-risk for malpractice liability (Jena et al., 2011). The MLM reports the average premium price in a county-year-specialty-insurer. Each observation in the MLM corresponds to the benchmark medical malpractice insurance premium charged by a specific insurer for a particular medical specialty in a given county and year. These premiums were adjusted for inflation using the CPI for All Urban Consumers: All Items, with 2015 as the base year.

For each specialty, we weight the premium data in a two-step process, because unweighted MLM data “understate the premium paid by a typical physician in these specialties” (Black et al., 2017). In the first step, we weight the MLM premiums by insurers’ market shares in a state using data from the National Association of Insurance Commissioners, as done in previous studies (Carrier et al., 2010). During this first weighting step, we aggregate data from the firm-county-year level to the county-year level. In the second stage of our weighting process, we further weight the county-year premium data by the number of physicians in a county-year-specialty cell to capture the effect on the average physician in a county-year-specialty cell.

Our study outcome is the weighted premiums at the county-year-specialty level. To account for the non-normally distributed premiums and for ease of interpretation, we use the natural logarithm of the weighted premiums as the dependent variable.

C. Explanatory Variables

Our main explanatory variable of interest is the state-level statutory repeal of noneconomic damage caps, which takes a value of 1 if a state repealed a noneconomic damage cap at year $t$, and 0 if a state still has a noneconomic damage cap through the study period. As discussed above, our treatment states include Georgia and Illinois, and each of them is compared with the 15 control states that maintained their caps through the study period. For the analysis of Georgia and the control states, the pre- and post-periods are 2005–2008 and 2009–2019; for the analysis of Illinois and the control states, the pre- and post-periods are 2005–2007 and 2008–2019.

Other Covariates

We include an array of county-level control variables, including unemployment rates, percent in poverty, median household income, percent of non-Hispanic white population, percent of population aged 20–44, percent of population aged 65 and over, reproductive-age women (aged 15–44) as percent of county population, and percent of the population uninsured. Information about these covariates is from Area Health Resources Files, except uninsurance rate, which is from the Census Bureau (U.S. Census Bureau, 2019; US Department of Health and Human Services, 2019).

D. Empirical Specification

To estimate the effect of repealing a noneconomic damage cap on medical malpractice insurance premiums, we employ a DD approach, comparing outcomes between treatment and control states from before to after repealing the cap. Our main DD specification is then denoted as follows:

$$\mathrm{l}\mathrm{n}(Y_{c,s,t})={{\beta }_0+\beta }_1{Treated}_s\times Pos{t}_t+X_{c,s,t}^{\prime }\theta +{\gamma }_c+{\delta }_t+{\epsilon }_{c,s,t}$$ (1)

Where $Y_{c,s,t}$ is the natural log of the weighted malpractice insurance premiums for county $c$ of state $s$ at year $t$. ${Treated}_s$ is a binary variable for treatment group status, which takes a value of 1 for Georgia and Illinois, and 0 for still capped states; $Pos{t}_t$ is a binary variable of the post-repealing period, which takes a value of 1 beginning in 2008 for Illinois, and beginning in 2009 for Georgia; ${Treated}_s\times Pos{t}_t$ is their interaction term, and its coefficient, ${\beta }_1$ is our main DD coefficient of interest. ${\gamma }_c$ and ${\delta }_t$ are the county and year fixed effects, and $X_{c,s,t}^{\text{'}}$ is a set of time-varying controls, including county-level unemployment rates, percent in poverty, median household income, percent of non-Hispanic white, percent of population aged 20–44, percent of population aged 65 and over, and reproductive-age women (aged 14–44) as percent of county population, and percent of the population without any health insurance. These demographic and economic controls intend to account for potential county- and state-specific time-varying factors, such as local economic conditions, given the treatment timing coincides with the end of the Great Recession. Finally, ${\epsilon }_{c,s,t}$ is the idiosyncratic error.

We are also interested in the dynamic effects of these repeals over time, so we extend (1) to the following event study specification:

$$\mathrm{l}\mathrm{n}(Y_{c,s,t})={\beta }_0+\sum _{k\ne -1}{\beta }_{1,k}{Treated}_s\times 1{\left\{\tau =k\right\}}_t+X_{c,t}^{\prime }\theta +{\gamma }_c+{\delta }_t+{\epsilon }_{c,s,t}$$ (2)

Where our event study coefficients, ${\beta }_{1,k}$, denote the leads and lags of our DD point estimates, $k$ years since a state first repealed its noneconomic damage cap in a circuit court. $\tau$ is the event time relative to repeal: $\tau =t$ – year of repeal. The reference period in event study analyses is thus 2007 for Illinois, and 2008 for Georgia, which is one year prior to the first circuit-court repeal of noneconomic damage cap in each state. There is only a single time-period difference in the initial treatment timing for Georgia and Illinois, so there would be little concern of negative weights stemming from heterogeneous timing of treatment (Callaway & Sant’Anna, 2021; Goodman-Bacon, 2021). Nevertheless, we focus our analysis by examining Georgia and Illinois separately, with the same set of control states in both regressions.

With only a single treated state being estimated separately, we must approach inference with caution. Econometric literature finds inflated Type I errors in DD estimates with traditional cluster-robust standard errors and few treated clusters (Bertrand et al., 2004; Ferman et al., 2019; MacKinnon & Webb, 2020). There are various inference methods that account for few treated clusters (Cameron et al., 2008; Conley & Taber, 2011; Donald & Lang, 2007). However, most of these approaches typically assume homoscedastic errors, when they are inherently heteroskedastic in our context due to differences in group sizes across treatment and control groups. We thus apply Ferman and Pinto’s (2019) inference approach, which is a cluster residual bootstrap procedure that can provide valid inference when there are few or even a single treated cluster, while also accounting for within-group clustering and heteroskedasticity stemming from variation in group sizes.

In addition to a regression approach, we apply the synthetic control method (Abadie, 2021; Abadie et al., 2010), aggregating our data to the state-year level, and using all the still capped states as our donor pool. We follow the recommended procedure for inference and compute the rank of Georgia and Illinois’ test statistics within the full distribution of placebo test statistics of donor states (Abadie et al., 2010; Abadie & L’Hour, 2021). We conduct synthetic control estimation using all of the pre-treatment period outcome lags, and in an alternative specification which only uses the outcome in 2005 to construct synthetic control weights as a recommend robustness check (Cavallo et al., 2013; Ferman et al., 2020; Galiani & Quistorff, 2017). Further details of our synthetic control method and test statistic are presented in Part C of the appendix.

We also leverage our county-level data and adopt an inverse probability weighted difference-in-differences (IPW-DID) specification as an alternative empirical strategy, which places a greater weight on counties that exhibit similar pre-treatment outcome trends to those counties in treated states, and less weight on counties that exhibit differential pre-treatment outcome trends from treated counties. We predict county-level propensity scores using logistic regression and the growth rate in outcome variables from 2005 to 2008 for Georgia, and 2005 to 2007 for Illinois.⁴ These are used to compute inverse probability weights.

E. Sensitivity Analysis

To examine how our results may vary across a different set of assumptions, we conduct seven robustness checks. As one sensitivity check, we run separate regressions with a smaller set of control states that still have noneconomic damage caps and are in the same census region as each treated state. For Georgia, the alternative control group consists of states that have noneconomic damage caps during the entire study period and are located in the South, including Maryland, Texas, and West Virginia. For Illinois, the alternative control group includes states that have still have noneconomic damage caps and are located in the Midwestern region, including Michigan, Ohio, and Wisconsin. Given their close geographic proximity to the treated states, these alternative control groups intend to account for region-specific time-varying confounders, such as regional demand or supply shocks that can be correlated with both the treatment (repeals) and the study outcomes (i.e., premiums). As a second sensitivity test, we estimate regressions omitting the appellate period between each treated states’ circuit court decision and supreme court decision to isolate the effect of binding repeals. Third, while we are careful to exclude controls that may theoretically induce collider bias and focus only on controls that increase precision, as an additional robustness check, we examine whether our results are sensitive to the inclusion of certain sets of controls. Specifically, we run the following alternative specifications that include: (1) only demographic controls, (2) only economic controls, and (3) no controls. Fourth, amid the rises in healthcare consolidation and physician employees among large hospital systems during our study period that may complicate the interpretation of our estimates, we re-run our specifications excluding counties that have large hospitals (with bed sizes > 300).

Fifth, to consider the possibility that our estimates may be driven by a few insurers with large market shares, we re-estimate our results without weighting premiums by state-level market shares. As a sixth sensitivity check, we assess how retaining counties with zero physicians and weighting at the state-year-specialty level as opposed to at the county-year-specialty level affects our estimates. Seventh, we estimate models including both never capped and still capped states using both regression and synthetic control methods to examine how broadening the definition of our counterfactual to include always treated (never capped) impacts our estimates.

IV. Results

A. Summary Statistics

Table 1 summarizes our study sample (N= 12,961 county-year observations) and covariates for the entire study sample and by treatment and control states. The table shows the weighted and unweighted statistics over the counties in our sample, following Lakdawalla and Seabury (2012). Weighted statistics are weighted by the total physician population in a county-year, while the unweighted statistics are not. The discussion hereafter is based on the weighted statistics. The average poverty rate in our entire sample is 14.37%; the average unemployment rate is 6.02%; the majority of the study population is non-Hispanic White at 58.99%; on average, 34.83% of the county populations are aged 20–44, while 12.83% are aged 65 and over. Finally, on average, 21.31% of the population are reproductive-aged women (aged 15–44), while, on average, 14.75% of the population is uninsured. Compared to the control counties, counties in Georgia have, on average, a higher poverty rate (16.91% vs 14.18%), higher unemployment rate (6.55% vs 5.79%), lower proportion of non-Hispanic White (49.16% vs 60.89%), higher population aged 20–44 (36.12% vs 34.61%), lower population of elderly aged 65+ (11.34% vs 12.99%), higher proportion of reproductive-aged women (22.36% vs 21.15%), and higher uninsurance rate (18.27% vs 14.63%). Compared to the control counties, counties in Illinois have, on average, a lower poverty rate (13.75% vs 14.18%) and lower unemployment rate (6.8% vs 5.79%).

Table 1.

Summary Statistics of Explanatory Variables

	(1) Georgia	(2) Illinois	(3) Still capped in the U.S.	(4) Still Capped in the South	(5) Still Capped in the Midwest	(6) Entire Sample
Panel A: Weighted statistics
% in Poverty	16.91	13.75	14.18	14.58	14.76	14.37
Median per capita Income ($)	44730.86	50145.32	46304.34	47974.41	43995.14	46758.45
% Unemployed	6.55	6.80	5.79	5.40	6.52	6.02
% Non-Hispanic White	49.16	55.92	60.89	46.82	74.16	58.99
% Population Aged 20–44	36.12	35.07	34.61	35.65	33.06	34.83
% Population Aged 65+	11.34	12.99	12.99	11.62	14.31	12.83
% Population Female Aged 15–44	22.36	21.44	21.15	21.83	20.56	21.31
% of Population Uninsured	18.27	13.22	14.63	19.04	10.30	14.75
No. of County-year Observations	1884	1277	9800	3515	3350	12961
Panel B: Unweighted statistics
% in Poverty	20.73	13.40	15.19	17.26	13.69	15.78
Median per capita Income ($)	30899.52	37768.69	38501.06	36976.56	36477.53	37412.55
% Unemployed	7.25	6.92	5.81	5.66	7.14	6.10
% Non-Hispanic White	63.73	88.01	77.40	65.15	89.99	76.48
% Population Aged 20–44	32.77	31.08	29.86	30.80	29.86	30.36
% Population Aged 65+	14.72	17.28	17.11	16.66	17.32	16.80
% Population Female Aged 15–44	19.78	18.60	18.05	18.59	18.29	18.33
% of Population Uninsured	19.51	10.63	17.22	22.10	10.90	16.96
No. of County-year Observations	2385	1530	13770	4995	3645	17685

Notes: Averages across counties within, each state group are reported. Panel A applies analytic weights using total physician counts across all three specialties in a county-year, while Panel B presents summary statistics without weights. Observation counts differ because county-years with, zero physicians are given zero weight.

We next present summary statistics of our outcome variable in Table 2 for both pre- and post-repeal periods for Georgia and Illinois, respectively. Compared to the control counties in the U.S. in the pre-repeal period, counties in Georgia have lower premiums for general surgery ($40,152.50 vs. $56,508.30), OB-GYN ($57,850.27 vs. $74,134.86), and internal medicine ($11,680.47 vs. $16,280.61). Compared to the control counties in the pre-repeal period, counties in Illinois have, on average, higher premiums for general surgery ($79,050.06 vs. $57,144.01), OB-GYN ($112,382.10 vs. $74,902.83), and internal medicine ($31,453.81 vs. $16,447.48). These pre-repeal differences in levels persist when defining the control states as those that are still capped in the same geographic region as a treated state. These underlying differences in the pre-period between the treatment and control counties motivate our inclusion of county fixed effects in all models.

Table 2.

Average premiums in counties in Georgia, Illinois, and Control states, pre- versus post-repeal period ($)

	Pre repeal	Post repeal	Difference (Post-Pre)	Difference-in-differences
General Surgery
Georgia	40152.5	44793.45	4640.949
Still Capped in the U.S.	56508.3	48777.76	−7730.547	12371.5
Still Capped in the South	58866.06	51293.39	−7572.67	12213.62
OB-GYN
Georgia	57850.27	64321.65	6471.37
Still Capped in the U.S.	74134.86	63485	−10649.86	17121.23
Still Capped in the South	82762.36	69935.16	−12827.19	19298.57
Internal Medicine
Georgia	11680.47	13384.58	1704.109
Still Capped in the U.S.	16280.61	15229.88	−1050.726	2754.835
Still Capped in the South	16210.32	15672.11	−538.206	2242.315
General Surgery
Illinois	79050.06	89831.36	10781.3
Still Capped in the U.S.	57144.01	49235.94	−7908.072	18689.37
Still Capped in the Midwest	64335.46	49865.94	−14469.51	25250.81
OB-GYN
Illinois	112382.1	120317.9	7935.801
Still Capped in the U.S.	74902.83	64149.9	−10752.93	18688.73
Still Capped in the Midwest	83292.13	70800.74	−12491.39	20427.19
Internal Medicine
Illinois	31453.81	33270.48	1816.668
Still Capped in the U.S.	16447.48	15273.72	−1173.765	2990.434
Still Capped in the Midwest	16357.51	15680.46	−677.0482	2493.716

Notes: All statistics are at the county-year level and weighted using a two-step process: first by insurance companies' market shares in a state-year, and then by the total number of physicians in a specialty in a county-year. The pre-repeal period is 2005–2008 and 2005–2007 for Georgia and Illinois, respectively, while the post-repeal period is 2009–2019 and 2008–2019 for Georgia and Illinois, respectively.

Table 2 also reports unadjusted DD estimates. While premiums are decreasing during our study period for still capped states, across our sample of counties and specialties, we find consistent evidence of an increase in premiums in Georgia and Illinois compared to that of control counties. For instance, premiums for general surgery increased by $4,641 in Georgia, compared with a decrease of $7,731 in the control counties, resulting in a DD estimate of $12,372. We observe relatively large effect sizes for OB-GYN ($6,471 vs. -$10,650 with a DD estimate of $17,121), and a smaller magnitude for internal medicine ($1,704 vs. -$1,051 with a DD estimate of $2,755). A similar pattern is observed in Illinois, whereby large magnitudes are observed for general surgery ($10,781 vs. -$7,908 with a DD estimate of $18,689) and OB-GYN ($7,936 vs. -$10,753 with a DD estimate of $18,689), and a smaller effect size for internal medicine ($1,817 vs. - $1,174 with a DD of $2,990).

We next present our multivariate regression results in the section below.

B. Regression Results

Table 3 reports DD estimates from Equation (1), with cluster residual bootstrapped p-values with Ferman and Pinto (2019) heteroskedasticity correction. We invert the test statistic to obtain asymmetric 95% confidence intervals and report these as well. Across all specialties, we find that premiums increased in Georgia and Illinois counties relative to the control counties after the noneconomic damage cap was repealed in each of the two states. Given that the dependent variable is the natural log of premiums, we convert the estimate to the implied percent change using ${100\times (e}^{\widehat{\beta }}-1)$. To retransform our estimates from the log-level models back to raw dollar levels, we employ a modified Duan smearing estimator that accounts for state-specific heteroskedasticity (Duan, 1983; Manning, 1998).⁵ Throughout our discussion, we will refer to these metrics.

Table 3.

Difference-in-differences estimates, by treated state and specialty

	(1) General Surgery	(2) OB-GYN	(3) Internal Medicine
Panel A: Treated: Georgia, Control: Still Capped States in the U.S.
DiD Estimate	0.179	0.208	0.150
95% CI	[0, 0.34]	[.05, 0.34]	[.10, 0.20]
Ferman and Pinto P-value	.079*	.014**	.002***
N	9037	7882	10633
Panel B: Treated: Georgia, Control: Still Capped States in the South
DiD Estimate	0.216	0.236	0.116
95% CI	[−.1, 0.30]	[−.3, 0.30]	[.05, 0.10]
Ferman and Pinto P-value	.243	.059*	<0.001***
N	3910	3555	4938
Panel C: Treated: Illinois, Control: States Still Capped in the U.S.
DiD Estimate	0.224	0.192	0.094
95% CI	[−.1, 0.55]	[−.2, 0.5]	[−.1, 0.30]
Ferman and Pinto P-value	0.134	0.103	0.159
N	8732	7434	10026
Panel D: Treated: Illinois, Control: States Still Capped in the Midwest
DiD Estimate	0.298	0.259	0.136
95% CI	[0.20, 0.60]	[−1, 0.30]	[−0.3, 0.25]
Ferman and Pinto P-value	<0.001***	<0.001***	0.039**
N	3901	3356	4302

Notes: Asymmetric 95% confidence intervals in [] are estimated using Ferman and Pinto (2019). All estimates include year fixed effects, county fixed effects, and time-varying county-level controls, including unemployment rate, percent in poverty, per capita income, percent of non-Hispanic white population, share of population aged 22 to 44, share of population, over the age of 65, share of population, female aged 15 to 44, and percent of uninsured.

^*p < 0.10,

^**p < 0.05,

^***p < 0.01

First, we report the adjusted DD results for Georgia in Panel A of Table 3. The repeal in Georgia is associated with an increase in premiums in general surgery by 19.6% relative to the control counties from pre- to post-repeal period (Column 1 of Table 3: Panel A), which is statistically significant at the 10% level and represents an increase of $9,015. The repeal is associated with a 23.12% and 16.18% increase in premiums for OB-GYN and internal medicine, respectively, which represent a $14,132 and $2,153 increase, respectively (Column 2 and Column 3 of Table 3: Panel A). The DD estimate for internal medicine and OB-GYN is statistically significant at the 5% level and 1% levels, respectively, while the estimate for general surgery is statistically significant at the 10% level.

Next, we report the adjusted DD results for Illinois in Panel C of Table 3. The repeal in Illinois is associated with an increase in premiums in general surgery by 25.11% relative to premiums in the control counties from pre- to post-repeal period, or a $12,310 increase (Column 1 of Table 3: Panel C), which is not statistically significant at the 10% level. The repeal is associated with a 21.17% and 9.86% increase in premiums for OB-GYN and internal medicine, respectively, which represent a $13,647 and $1,416 increase, respectively (Column 2 and Column 3 of Table 3: Panel C), which are statistically indistinguishable from 0 at the 10% level.

The main event study estimates for Georgia are reported in Panel A of Figure 1 (with Ferman and Pinto (2019) p-values reported in Panel A columns (1)-(3) of Table B10 in the Online Appendix). Prior to the repeal, all event study point estimates are not statistically significant, with the exception of event time −4. An increase in premiums is observed across specialties between the circuit and supreme court decision, and the effect size grows across specialties after the supreme court decision. We note here that there is a secular increasing trend in premiums prior to Georgia’s repeal. While there may be various factors at play, we suspect that this may be attributable in part to Georgia’s periodic payment reform in 2005, where large damages can be awarded in periodic payments rather than in lump sum. The introduction of this policy around this time may have worked to create lower premiums in the pre-period relative to the control group.

Figure 1. Event Study Estimates.

Notes: 95% confidence intervals with standard errors clustered at the state-level. The earlier vertical dashed in each graph depicts the timing of circuit court repeals, while the later dashed line depicts the timing of state Supreme Court repeals.

The event study estimates for Illinois are reported in Panel B of Figure 1 (with Ferman and Pinto (2019) p-values reported in Panel B columns (1)-(3) in Table B10 of the Online Appendix). Prior to repeal, all event study point estimates are statistically insignificant. We observe a similar pattern between Illinois and Georgia: An increase in premiums is observed across specialties between the Circuit and the State Supreme Court decision; the increase becomes larger after the Supreme Court decision.

While not the main focus of our study, we examined the association between partial, incomplete, or confounded repeals and premiums, by specialty, in Table A2 of the Online Appendix. In contrast to Georgia or Illinois, we find insignificant effects of the repeals on premiums across all specialties among the states with partial, incomplete, or confounded repeals.

Our IPW-DID results are reported in Table B2 of the Online Appendix, with logit estimates reported in Table B3. Our results for Illinois are largely unchanged with small decreases in magnitude and no changes in statistical significance. Effect sizes for Georgia decrease when using still capped states in the U.S. but increase when using a group of neighboring states as the control group.

C. Synthetic Control Results

We first present in Figure 2 the results from a specification that uses all of the pre-treatment outcome lags to construct the synthetic treated states, with the implied unit-specific weights reported in Table B13 in the appendix. Panel A of Figure 2 shows the raw trends in premiums for Georgia and its synthetic control while Panel B of Figure 2 indicates the raw trends in premiums for Illinois and its synthetic control are presented. Together, these two panels demonstrate that in all specialties in both Georgia and Illinois, there is a clear increase in premiums after repeals, compared to premiums of each respective state’s synthetic control, with the exception of OB-GYN in Illinois. Prior to repeals, trends in premiums between treated states and synthetic control states are parallel or nearly identical. However, we note that pre-treatment fit may be imperfect for internal medicine in Illinois.

Figure 2: Synthetic Control Estimation using All Pre-Treatment Outcome Lags.

Notes: The outcomes are the logged premiums for general surgery, OB-GYN, and internal medicine. The dashed vertical line represents the circuit court decision on repealing each treated state’s noneconomic damage cap. Panel A provides the raw trend for Georgia and its synthetic control, while Panel B shows the raw trend for Illinois with its synthetic control.

We then present in Figure 3 each treated state’s test statistic in relation to the full distribution of placebo test statistics, using all of the pre-treatment outcome lags, showing a right-sided test. We find that OB-GYN and internal medicine have the highest test statistic in Georgia and OB-GYN the third largest in Illinois relative to placebo test statistics. In Illinois, general surgery and internal medicine have the third-and fourth-highest test statistics, respectively.

Figure 3: Placebo Test Statistics using All Pre-Treatment Outcome Lags.

Notes: Test statistics are calculated for each state. Treated states are highlighted in red.

We next turn to our synthetic control results using only the 2005 outcome lag as a predictor variable to construct a synthetic Georgia and Illinois, the results of which are presented in Figures 4 and 5, respectively. In Figure 4, we note that using only the outcomes from 2005 can be a reasonably valid predictor, as the synthetic controls for Georgia and Illinois covary closely with actual pre-treatment group trends, with the exception of internal medicine in Illinois. We note here that the test statistic for general surgery in Illinois rises to first in rank when using only the 2005 outcome lag as a predictor.

Figure 4: Synthetic Control Estimation using 2005 Pre-Treatment Outcome Lag.

Notes: The outcomes are the logged premium for general surgery, OB-GYN, and internal medicine. The dashed vertical line represents the circuit court’s decision on repealing each treated state’s noneconomic damage cap. Panel A provides the raw trend for Georgia and its synthetic control, while Panel B shows the raw trend for Illinois with its synthetic control.

Figure 5: Placebo Test Statistics using 2005 Pre-Treatment Outcome Lag.

Notes: Test statistics are calculated for each state. Treated states are highlighted in red.

The results from our synthetic control analysis are broadly consistent with our main findings. While a p-value, by construction of our test statistic, would be somewhat uninformative given the small number of donor states, we find that across both of our synthetic control specifications, OB-GYN and internal medicine always ranks first among the distribution of placebo test statistics in Georgia (Figure 3 and 5). While the results for general surgery are somewhat more sensitive to specification for inference, the results always indicate a positive effect.

D. Sensitivity Analysis Results

The results for our alternative control group – which includes only the states in close geographic proximity to a treated state – are presented in Panel B and D of Table 3, and Figure 6. We find that the effect sizes and statistical significance are generally greater when using this set of closer controls across specialty and treated state. The increase in magnitudes is most pronounced for general surgery and OB-GYN – where we observe an increase in magnitudes ranging from 0.028 to 0.074 – compared to internal medicine, which decreased in magnitude by 0.034 in Georgia and increased by 0.042 in Illinois. We note that changes in statistical significance are observed primarily in Illinois.

Figure 6. Event Study Estimates with Alternative Control Groups.

Notes: 95% confidence intervals reported with standard errors clustered at the state level. The control group in Panel A are Southern states that are still capped, while the control group in Panel B are Midwestern states that are still capped.

Table B4 in the Online Appendix summarizes the results from our second sensitivity analysis, where we drop the period between the circuit court and State Supreme Court decisions in each treated state. As expected, we find that the effect of a binding decision by State Supreme Courts are stronger in magnitude and statistical significance than when including the anticipatory period for both states. Across the three specialties for Georgia and Illinois, magnitudes increase with the exclusion of the anticipation period.

Table B5 in the Online Appendix summarizes our regression results from a third sensitivity test that excludes groups of control variables. We note that excluding either economic controls or only demographic controls does not appear to impact our point estimates substantially. However, excluding all controls increases the noise in our estimates sufficiently to make estimates for Illinois statistically insignificant only at the 10% level for general surgery and OB-GYN with close controls. Throughout our analyses, we excluded potentially problematic controls that could induce collider bias; moreover, coefficient effect sizes remain relatively stable regardless of the exclusion of controls. We thus believe that our covariates contribute to our estimates predominately through increases in precision.

We next report a fourth sensitivity test that excludes counties that contain large hospitals with more than 300 beds in Table B6. As physicians are more likely to be employed in large hospital systems amid the rise in healthcare consolidation over the study period, we run this sensitivity test to account for the possibility that the rise in physician employees could confound the results. We find that our effect sizes and statistical significance tend to be generally unchanged. However, general surgery becomes statistically significant at the 5% level in Illinois (Panel C) when it was statistically indistinguishable from zero at the 10% level prior to the exclusion of counties with large hospitals.

Table B7 reports our fifth sensitivity test, which reports estimates without weighting premiums by state-level insurer market shares. We find that not scaling premiums by market shares tend to shrink our effect sizes, though statistical significance remains unchanged.

Table B8 reports our sixth sensitivity test, which assesses the stability of our estimates by weighting by state-year-specialty as opposed to county-year-specialty. On the one hand, weighting by state-year-specialty is beneficial because it would retain the sample of county-year-specialty without physicians, which could reduce noise in our estimates. On the other hand, weighting at the state-year level may also obfuscate important sub-state variation in the treatment effect. If repealing noneconomic damage caps has differential impacts across counties with different numbers of physicians (e.g., due to risk pooling being more feasible in counties with more physicians), then weighting by state-year-specialty will ignore county-level variations in physician numbers, potentially leading to an overestimate (or underestimate) of the treatment effect, or at least, a treatment effect that is different from what we are substantively interested in from a policy perspective. Evidently, we see some evidence of larger treatment effects when weighting by state-year-specialty as opposed to county-year-specialty for regional control group specifications.

Finally, in Tables B9, B11, B12, Figures B1 and B2, we report our seventh sensitivity test, which includes both never treated (still capped) and always treated (never capped) states as the control group. We find that our regression and synthetic control estimates (when using all pre-treatment outcome lags) are no longer statistically distinguishable from zero at the 10% level (Table B9 and Table B11, respectively). When using only 2005 as the pre-treatment outcome lag, as reported in Table B12, OB-GYN and general surgery in Georgia, and general surgery in Illinois are ranked first out of 39 in several time periods in in-space placebo tests, implying a right-sided p-value of 0.026. The trends in outcomes for the treated group outcome and synthetic controls for a specification that includes never capped, as well as the distribution of test statistics for the overall treatment effect, are reported in Figures B1 and B2.

Taken together, our sensitivity analyses suggest that across all specifications and the three physician specialties, medical malpractice insurance premiums tend to increase in response to the repeal of a noneconomic damage cap. These increases are most pronounced in magnitude in general surgery and OB-GYN.

V. Conclusion and Discussion

This study is the first to examine the effect of repealing noneconomic damage caps on medical malpractice insurance premiums, using the circuit and supreme court decisions in Georgia and Illinois as case studies. Consistent with the predictions of our conceptual framework, our empirical analysis finds large and persistent increases in malpractice insurance premiums following the repeals. The magnitudes that we observe are larger in OB-GYN and general surgery, or approximately 20–23%, and smaller in internal medicine at approximately 16%. A summary of the literature finds that states that introduce noneconomic damage caps experience a decrease in average premiums by approximately 6–13% (Mello et al., 2011). This suggests that, compared with the introduction of noneconomic damage caps, repealing the caps results in behavioral responses remarkably larger in magnitude, providing the first suggestive evidence of asymmetric effects between introducing and repealing damage caps. Given that malpractice insurance premiums reflect physician liability risk and practice costs (Mello et al., 2010), states considering the repeal of their caps may need to understand the potential ramifications of their policy actions for malpractice insurance premiums and subsequent consequences for physician practice and patient health care.

Despite these findings, our study has several notable limitations. First, our data on premiums reflect both demand-side physician behavior and supply-side insurance firm behavior, but we are unable to disentangle these two forces. Similarly, our conceptual framework suggests that repealing a noneconomic damage cap may increase both the size and the probability of an expected loss and subsequently lead to an increase in our measure of premiums. Although we do not have data about the size and perceived probability of an expected loss, our empirical analyses suggest that, while any of these potential mechanisms could be at play, the direction of the effect is likely to be positive.

Second, while we take great care in our analysis by employing a DD specification and implicitly testing for parallel trends, using county and year fixed effects and county-level covariates, and ensuring the absence of confounding policies for both Illinois and Georgia, we note that the repeal of a noneconomic damage cap was not randomly assigned and is thus subject to the possibility of time-varying unobserved endogeneity.

Third, our results for Illinois are somewhat sensitive to our choice of control states: while the results across specialties in the state are statistically insignificant when including a wider set of control states, restricting our control states to those in close geographic proximity to Illinois yields highly statistically significant results across all the specialties. However, this result is not too surprising, given the plausibility of closer states being a better counterfactual and suggests that our baseline estimates using a broader set of control states is likely a conservative estimate that is downward biased. This is supported by the fact that including the widest set of control states – both still capped (never treated) and never capped (always treated) -- makes our regression estimates statistically insignificant, with the exception of general surgery and internal medicine in Georgia in our sparse synthetic control specification, and general surgery in Illinois.

Finally, a limitation of the MLM dataset is that it only includes the individual malpractice insurance market. Physicians are more likely to be employed in large hospital systems amid the rise in healthcare consolidation over the study period. As part of these employment arrangements, physicians are more likely to receive malpractice insurance through their employers’ captive insurers. Our data does not capture this variation in premiums in larger health systems and is thus limited in its ability to reflect broader settings beyond the individual malpractice insurance market. The rise in physician employees may also add an additional level of complexity to the interpretation of our results if high risk physicians are more likely to join large healthcare systems when caps are repealed. Such a change in the composition of physicians in the individual market may lead to a form of selection that decreases insurers’ perceived probability and size of losses (assuming physicians’ risk levels are observable). Nevertheless, our robustness checks that exclude counties with large hospitals suggest that such concerns are negligible.

Despite these caveats, the magnitudes of our estimates are consistently large and positive across all specifications and outcomes. Moreover, the magnitudes that we observe remain substantially larger than those reported in the literature on the introduction of noneconomic damage caps, suggesting a potential asymmetric effect. Taken together, these results may warrant attention from policymakers, physicians, researchers, and malpractice insurance companies.

Our findings point to several directions for future research. First, it may be of interest for future studies to disentangle the supply-side behavior from that of demand-side responses, provided that such data are available. Additional measures on either the price of insurance coverage or the amount of insurance coverage would elucidate the mechanisms by which we observe an increase in premiums. Second, it may be worthwhile to study how other outcomes, such as healthcare costs, defensive medicine, physician supply, and patient health, change after the repeal of a noneconomic damage cap. Third, it is plausible that the rise in physician employees during our study period could have led to an increase in the purchase of supplemental coverage among physicians in large hospital systems, which could influence medical malpractice insurance premiums.⁶ The Medical Liability Monitor is not granular enough to permit us to study this question, and it may be a pertinent direction for future research.

Data Availability Statement:

The Database of State Tort Law Reforms (7^th edition), is publicly available at https://law.utexas.edu/faculty/ravraham/dstlr.php . The malpractice premium data were purchased from Medical Liability Monitor, which conducts annual survey of medical malpractice insurance rates.