22. the impact on non-economical damages caps on obstretics
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The impact of non-economic damages caps on obstetrics:
Incentives versus practice style
Anca Cotet-Grecu *
Department of Economics and Legal Studies, Seton Hall University, 400 South Orange Avenue, South Orange, NJ 07079, United States
1. Introduction
There is a good deal of research on the impact of
malpractice cost and tort reform on medical practice,
including the field of obstetrics, but not all of the findings
are consistent. For instance, one strand of literature
indicates that higher malpractice premiums are associated
with an increased use of C-sections (Dubay et al., 1999;
Grant and McInnes, 2004), but some researchers find that
noneconomic damage caps, which decrease malpractice
premiums, are associated with higher rates of C-sections
(Currie and MacLeod, 2008).
This paper makes several contributions to this litera-
ture. First, I revisit two of the main findings of this
literature: that non-economic damages caps1 are associat-
ed with entry into the field of obstetricsgynecology (Klick
and Stratmann, 2007) as well as with higher rates of C-
sections (Currie and MacLeod, 2008). Using county-level
data, I find that the results hold for the 19892001 reforms,
the original period investigated by Currie and MacLeod
(2008), but not when the more recent reforms are added,
for the years spanning 19892010. Estimates lack external
validity when the researcher fails to account for all margins
of choice. I test whether general equilibrium effects
explain this observation. I find that the observed change
in C-section rates prior to 2002 is driven by areas with
significant entry and that such a change is not present in
the remaining areas where there is no/less scope for
mobility. A similar pattern exists in the case of prenatal
care initiation and of prenatal visits.
Second, I find that these changes in procedures are
associated with differences in health outcomes that follow
a similar pattern. Between 1989 and 2002, non-economic
Economics and Human Biology 17 (2015) 2941
A R T I C L E I N F O
Article history:
Received 13 May 2014
Received in revised form 11 December 2014
Accepted 11 December 2014
Available online 20 December 2014
JEL classification:
I12
I18
K13
Keywords:
Non-economic damages caps
Ob-gyn
C-sections
Infant outcomes
A B S T R A C T
This paper uses 19892010 county-level data to reexamine the effect of non-economic
damages caps on the field of obstetrics. Previous literature found that caps on damages
lead to both changes in the number of physicians and changes in treatment patterns. This
paper investigates whether the changes in procedures are attributable to changes in
incentives or to selection when new entrants could have a different practice style than
incumbents. First, I find that the relationship between non-economic damages caps and
the number of physicians and procedures identified in previous literature is not robust to
the inclusion of the newer policy changes. Second, over the period when such changes
were observed, the impact on procedures is concentrated in areas with the greatest
changes in the number of obstetricians/gynecologists per capita, suggesting that most of
the effect on procedures is driven by differences in practice style between entrants and
incumbents.
2014 Elsevier B.V. All rights reserved.
* Tel.: +1 973 761 9356.
E-mail address: [email protected] Non-economic damages compensate for past or future non-economic
losses, such as pain, suffering, emotional distress, mental anguish,
disfigurement, physical impairment, loss of consortium, loss of compan-
ionship, loss of parental guidance, loss of enjoyment of life, loss of society,
humiliation, embarrassment, inconvenience, injury to reputation, and
other such losses (Pace et al., 2004).
Contents lists available at ScienceDirect
Economics and Human Biology
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http://dx.doi.org/10.1016/j.ehb.2014.12.002
1570-677X/ 2014 Elsevier B.V. All rights reserved.
http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002mailto:[email protected]://www.sciencedirect.com/science/journal/1570677Xhttp://dx.doi.org/10.1016/j.ehb.2014.12.002http://dx.doi.org/10.1016/j.ehb.2014.12.002http://www.sciencedirect.com/science/journal/1570677Xmailto:[email protected]://dx.doi.org/10.1016/j.ehb.2014.12.002http://crossmark.crossref.org/dialog/?doi=10.1016/j.ehb.2014.12.002&domain=pdfhttp://crossmark.crossref.org/dialog/?doi=10.1016/j.ehb.2014.12.002&domain=pdf -
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damages caps are associated with fewer births with low
Apgar scores and a decrease in the incidence of neonatal
injury deaths despite the higher rate of C-sections. These
findings are suggestive of an improvement in fetal health.
All these results are driven by areas with significant entry
into the field of obstetrics and are not robust to extending
the sample through 2010.
One
explanation
relies
on
the
observation
that
liability-sensitive physicians choose to locate where malpractice
liability is low. When non-economic damages caps reduce
liability, the resulting increase in competition in these
areas could improve access to care, leading to better fetal
health. At the same time, entrants could have a different
practice style than the average provider in a particular
area. For instance, if liability-sensitive physicians have
poorer diagnostic skills and use surgical intervention more
often (Currie and MacLeod, 2013), states with higher
proportions of entrants would experience larger increases
in C-section rates. This mechanism can explain why the
impact of non-economic damages caps does not work in
the
opposite
direction
of
the
effect
of
an
increase
inmalpractice liability. This paper thus contributes to the
literature by reconciling apparently conflicting findings in
previous research. It is plausible that most of the change in
treatment patterns due to non-economic damages caps is
driven by selection and not by the impact of changes in
incentives.
This mechanism can also explain the lack of robustness
of the estimated effect of non-economic damages caps over
time. More recent reforms might not be associated with
significant entry, possibly because the scope of mobility
decreases as more states pass such legislation or because
successful past repeals reduce expected gains from
mobility.
2. The economics of tort reform
Where medical liability insurance is an important
component of the operating cost of a medical practice,
legislation that reduces malpractice insurance premiums
should increase the profitability of the medical profession
and induce entry into the medical field. Non-economic
damages caps reduce insurer payouts (Sloan et al., 1989;
Avraham, 2007; Hyman et al., 2009) and the probability of
lawsuits (Kessler and McClellan, 1997; Browne and Puelz,
1999) and, thus, they are expected to increase the supply of
medical
care.Previous literature has found evidence of an increase in
the number of doctors (Encinosa and Hellinger, 2005;
Kessler et al., 2005; Matsa 2007) and more so in high-risk
specialties (Klick and Stratmann, 2007) such as obstetrics
gynecology. This evidence is not always consistent, howev-
er, and Yang et al. (2008) find no evidence that tort reform
increased the number of obstetriciangynecologists.
Nevertheless, even when the number of physicians does
not change, a decrease in cost could still shift the supply of
medical care and decrease prices. As predicted, the changes
in the cost structure of the industry because of non-
economic damages caps (and other tort reforms) have been
found
to
be
associated
with
higher
prevalence
of
healthinsurance coverage for the most price-sensitive groups
(Avraham and Schanzenbach, 2010). This in itself would
lead us to believe that tort reforms lead to better health.
Previous literature, however, has found only very limited
evidence of health improvements. In particular, Klick and
Stratmann (2007) found that non-economic damages caps
are associated with a reduction in black infant mortality
rates. One proposed explanation is that changes in
physicians
incentives
lead
to
changes
in
treatmentpatterns (Currie and MacLeod, 2008) that are not
necessarily associated with better health (Kessler and
McClellan, 1996) and may in fact lead to more medical
mistakes (Cotet, 2012).
The case of obstetrics is especially confusing because of
apparently conflicting results. There is some evidence that
C-section rates are responsive to financial incentives
(Gruber et al., 1999), but other evidence indicates that
C-sections are not sensitive to medical malpractice risk
(Kim, 2007). Previous literature found that higher mal-
practice premiums are associated with an increased use of
C-sections (Dubay et al., 1999; Grant and McInnes, 2004).
At
the
same
time,
there
is
evidence
that
noneconomicdamages caps, which decrease malpractice premiums
(Thorpe, 2004; Danzon et al., 2004), are associated with
higher rates of C-sections (Currie and MacLeod, 2008).
There are arguments to be made for both sets of results.
C-sections could be used to protect against malpractice
claims that argue that negative infant outcomes arose from
waiting too long to perform surgery (see DAttilo versus
Viscarello 2011, which resulted in a $58 million award; or
Fielding and Martinez versusJohn Hopkins Hospital 2012,
which resulted in a $55 million award). Therefore, C-
sections could be one more way physicians practice
defensive medicine. At the same time, C-sections entail
risks.
They
could
lead
to
injury
or
infections
and
couldaffect future fertility, all of which could lead to malpractice
lawsuits. Thus, physicians may be reluctant to perform C-
sections in an effort to avoid litigation.
Ultimately, whether C-sections rates are too high boils
down to determining whether at the margin additional
procedures are associated with a net benefit. Previous
literature found no evidence that higher rates of C-sections
are associated with any changes in infant health (Baicker
et al., 2006), findings that do not appear to suggest that
physicians avoid C-sections because of potential liability.
In addition, there may be general equilibrium effects. To
the extent that the litigiousness of a place affects
physicians
scope
of
practice
and
location
choices,
changesin working environment driven by the decline in the
likelihood of being sued due to non-economic damages
caps could lead to geographical mobility (Matsa, 2007).
Such mobility could differentially alter treatment choices
and outcomes in the affected areas. Because the scope of
mobility decreases as more states pass such legislation or
fall under a federal tort reform, predictions based on early
reforms may under/overestimate the impact of tort reform.
Interestingly if the estimated effect of caps is driven by
such mechanisms, all theories regarding the use of C-
sections predict the same outcome. If a high rate of C-
sections performed indicates a risk-taking physician, lower
liability
could
attract
the
most
risk-taking
physicians,leading to an increase in C-sections in states with caps. In
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fact the same result would occur if C-sections were a form
of defensive medicine. A risk-adverse physician that
performs many C-sections might find a state with caps
particularly attractive. C-sections might also increase
where competition improves pregnancy health and more
difficult pregnancies result in live births if these additional
births are more likely to be associated with surgical
deliveries.
Alternatively,
if
the
most
liability
sensitivephysicians that drive the increase in supply tend to have
poorer diagnostic skills they may perform differentially
more C-sections (Currie and MacLeod, 2013). In all these
situations, there would be an amplification effect: the
coefficients obtained would overestimate the incentive
effect.
3. Econometric strategy
The following equation describes the empirical model2:
Yct uCAPs;t1 bXc s t ac gtr vst ect (1)
where s stands to state, c for county, r for region, t for yearand ectis the stochastic error term.
Yctcould be one of the following outcomes variables in
county c year t: obstetricians per 10,000 women; prenatal
visits per live births; C-section rate among live births;
births per 100 women of fertile age (1544 years old);
percent mothers who initiated prenatal care during the
first trimester, second trimester, third trimester, or did not
receive prenatal care; percent premature births (
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overall level of health of the population in a county do not
confound the effect of non-economic damages caps. The
equation also includes year fixed effects, gtr, meant tocapture time-varying differences in the dependent variable
common to all counties, such as changes in federal-level
healthcare policies. Because there are regional differences
in physicians practice style that may change over time the
year
effects
are
allowed
to
vary
by
region.State-specific trends in medical-care utilization rates
could impact a states likelihood to adopt a non-economic
damages cap. To control for such a possibility, the model
includes state-specific time trends, vst. Controlling forthese trends reduces the burden of the assumption of
reforms exogeneity. Conditional on county, region by year
fixed effects, and state-specific trends, the us are identifiedfrom year-by-year changes in legislation, after controlling
for shocks common to all counties, differential shocks to
different regions, and state-specific trends.
One more issue about the estimation strategy should be
mentioned. The independent variable of interest varies
only
at
the
state
level.
Moreover,
it
could
be
that
the
errorterms are correlated within states over time, although the
fact that laws are also repealed during the period
investigated is useful for identification because it helps
ensure that general trends in outcomes are not confounded
for the effect of caps. Nevertheless, misspecification of the
autocorrelation process can lead to downward bias in the
standard-error estimates (Bertrand et al., 2004). Conse-
quently, robust standard errors clustered at the state level
that allow for heteroskedasticity and autocorrelation of
unspecified form are calculated and reported throughout
the paper6.
The key identifying restriction in this paper is that the
adoption
of
non-economic
damages
caps
is
exogenous.
Theliterature indicates that the timing of the adoption is mostly
the resultof vagaries of the political process (Rubin,2005).
A significant portion of the reforms is not specific to
medical malpractice, but is instead broad tort reform,
applying to accidents and product liability as well
(Avraham and Schazenbach, 2010). Thus, it is unlikely
that tort reforms were passed in response to changes in
the obstetrics practice (Currie and MacLeod, 2008).
Numerous papers, among which Rubin and Shepherd
(2007), Avraham and Schazenbach (2010), and Cotet
(2012) are just a few examples, investigated this point
using a variety of balancing tests and graphical evidence
and
found no
evidence
of
endogeneity
so
I
will
not
repeatthe exercise here. However, because this paper investi-
gates the robustness of the results over time in Table 1, I
present summary statistics indicating whether the
distribution of observable covariates is similar in all
period investigated (Heckman and Hotz, 1989).
4. Data
The physician data comes from the Area Resource File
(ARF), which contains county level information about the
number of obstetricgynecologists starting in 1995. This
data are also available separately by age.
For the investigation of obstetric procedures and birth
outcomes I use the 19892010 National Center for Health
Statistics (NCHS) Natality Files, which provide a census of all
births. This dataset contains information on the newborns
health, the demographic characteristics of the parents, the
pregnancy
history
of
the
mother,
and the
prenatal carehistory of the mother. In addition, these data provide
information about childbirth procedures. Over the period
of thisstudy, therewere significant changes in thecontent
of the birth certificate. As a result, some of the data from
the revised (2003) andunrevised (1989) birth certificates
may not be comparable. I concentrate on C-sections
because these data are consistent over the entire period
investigated, while the prevalence of stimulation of labor
may notbe fullyconsistent7. The dataon health outcomes
is fully consistent over time. Although some states revised
theprenatalcare initiationquestions on birth certificates I
retain the data on prenatal care initiation, an outcome
variable.
If the measurement error
in
this dependentvariable is not correlated with the independent variables,
it does not bias the estimates. All regressions that use
Natality data control for an indicator variable for the
states that revised birth certificatedafter the revision. All
conclusions drawn based on results obtained using data
from thetwo certificates combined are reinforced byother
empirical tests usingonly data prior toany revision in any
states, i.e. before 2003.
Because in some regressions the period investigated is
quite long (22 years) and there are changes over time in the
prevalence of multiple births, I retain only the sample of
singleton births. This ensures that the observed changes in
the
prevalence
of
C-sections
and
poorer
birth
outcomes
arenot driven by trends in multiple births known to be more
likely to be associated with surgical delivery and higher
incidence of prematurity and low birth weight. The
retained data are then collapsed at county level to allow
the investigation of the differential effect of tort reform
function of local characteristics. These data are then
merged with the state legislative data.
State by state legislative data are taken from Avrahams
(2011) Database of State Tort Law Reforms (DSTLR
4 dataset). The impact of the law is measured by
introducing a dummy variable indicating whether the
state has a cap on non-economicdamages in a given year,
regardlessof
the
value
of
thecap.
If
theeffective
date
of
thereform was on or after July 1st, it was coded as belonging
to the following year.
Although, as Avraham (2011) indicates, many states
experimented with non-economic damages caps before
1989, there was significant legislative activity both in the
period of reference, 19892001, and in recent period,
20022010. Specifically, given that, as will be shown
below, this analysis suggests there is a one-year lag in the
effect of caps, the investigation of the 19892001 birth
cohorts covers fifteen reforms: six instances of caps
6
The
standard
errors
are
essentially
the
same
when
clustering
by
stateand year; results are available on request.
7
Some
results
regarding
the
prevalence
of
induction
are
discussed
inthe paper. The data on induction is consistent over the entire period.
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adoptions (IL 1995, WI1995, MT 1996, ND 1996, SD, 1996,
OH 1997) and nine instances of caps repeals (WA 1989, MN
1990, NH 1991, WI 1991, OH 1992, AL 1993, IL 1998, OH
1998, OR 2000) as shown in Fig. 1. The analysis of 1989
2010 birth cohorts covers an additional ten reforms: nine
instances of adoptions (FL 2003, MS 2003, NV 2003, OH
2003, OK 2004, TX 2004, GA 2005, IL 2006, SC 2006) and
one repeal (IL 2008) as shown in Fig. 2.
The source of fetal death data is the NCHS Fetal Deaths
Files. At the time of this research Fetal Death data are
available only until 2006. Because different states have
different gestation thresholds for reporting fetal death, I
retain only the records indicating a gestation that would
ensure data reliability and comparability across states.
Table 1
Summary statistics.
19892001 19892010
Mean Standard error Mean Standard error
Ob-gyn 2.420 (1.473) 2.440 (1.454)
C-sections 21.057 (4.369) 24.375 (6.223)
Prenatal visits 11.298 (1.139) 11.277 (1.181)
Prenatal care initiation
1st Trim 80.083 (8.583) 79.417 (9.538)
2nd Trim 15.283 (6.014) 15.794 (6.711)
3rd Trim 3.230 (2.141) 3.394 (2.346)
None 1.404 (1.608) 1.396 (2.087)
Births 6.380 (2.635) 6.438 (2.719)
Gestation
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Specifically, I use fetal deaths per 1000,000 women aged
18448 occurring after 28 weeks of gestation9.
The source of neonatal mortality data is the Com-
pressed Mortality Files compiled by NCHS. They contain
information
from
all
death
certificates
filed
in
the
50
statesand the District of Columbia. The per-capita personal
income data come from the Bureau of Economic Analysis.
The county level population data by gender, race and age
come from National Center for Health Statistics (NCHS)
Bridged Race Population Estimates. County level hospital
data as well as data regarding urban-rural states come
from the Area Resource File. The state-level education and
marital status data for women come from the Current
Population Survey, March Supplement.
5. Results
5.1.
Main
results
5.1.1. Effect on supply
First I show results obtained for the period running up
to and including 2001, and subsequently I extend the
period to cover all reforms passed until 2010. The
2001 cut-off was chosen to match the period used by
previous literature as closely as possible. Both Klick and
Stratmann (2007), who find effects on physicians in high-
risk specialties, such as obstetrics and gynecology, and
Currie and MacLeod (2008), who find effects on C-sections,
use data up to and including 2001.
In Table 2, I present results suggesting that during the
19952001
period,
non-economic
damages
caps
wereassociated with an increase in the number of ob-gyns per
10,000 women. The adoption of non-economic damages
caps is associated with 0.103 more ob-gyn per 10,000
women, the equivalent of a 4.26% increase in the supply of
ob-gyn. This estimate is very close to the Klick and
Stratmanns (2007) findings of a 4.1% increase in supply of
physicians in high-risk specialties. However, the results do
not hold when the period is extended to 2010. The
estimated effect during the period 20022010 is signifi-
cantly different from the estimated effect during the pre-
2002 period (p-value 0.049). It is possible that scope of
mobility decreases as more states pass such legislation. An
alternative
explanation
is
that,
over
time
the
high
rate
ofsuccessful repeals decreased the trust that a policy will
Table 2
Non-economic damages caps and the supply of medical care: the case of obstetrics.
Dep. Var. Ob/Gyn [1] Prenatal visits [2] Cesarean [3]
Panel A: 19892001
NE Cap 0.103** (0.049) 0.102*** (0.037) 0.412** (0.200)
Obs. 17,696 32,458 32,582
Panel B: 19892010
NE
Cap
0.033
(0.030)
-0.174
(0.138)
0.453
(0.275)Obs. 40,048 54,496 54,728
Panel C: 20022010
NE Cap 0.005 (0.016) -0.147 (0.147) 0.254 (0.182)
Obs. 22,352 22,038 22,146
The dependent variables are: obstetriciansgynecologists per 10,000 women in column 1, average number of prenatal visit per live birth in column 2, and C-
sections per 100 live births in column 3. Due to data availability column 1 only uses the data after 1995. NE Cap stands for non-economic damages caps
reforms. The regressions reported in column 1 control for percent white (omitted), percent black, and percent other race; the age structure: percent under
15 years old (omitted), 1544, 4564, 65 and older; log of county income per capita; and for state level variables such as womens education: percent with
less than a high-school degree (omitted), percent with a high-school degree, percent with some college, and percent with a college degree or more
education; and marital status. The regressions reported in columns 2 and 3 control for birth parity: first child, second child, third child, fourth child, fifth or
subsequent child (omitted); gender; mothers age: under 25 (omitted), 2534; over 35 years old; mothers education: less than high-school education
(omitted), high-school, some college, college or more; mothers race: white (omitted), black, other race; Hispanic; marital status; and log of county income
per capita. All regressions control for joint and several liability reforms, punitive damages reforms, collateral source reforms, total damages reforms. All
regressions include county fixed effects, year fixed effects that are allowed to vary by region and state specific time trends. The regressions reported in
column 1 are weighted by the number of women in a county-year. The regressions reported in columns 23 are weighted by the number of live births in acounty-year. Robust standard errors clustered at state level are reported in parentheses.
* Significant at 10% significance level.
** Significant at 5% significance level.
*** Significant at 1% significance level.
Fig. 2. Non-economic damages caps changes legislative changes 2002
2010 (light gray for adoptions, dark gray for repeals, black for states that
both adopted and repealed a cap).
8 This specification is preferable to using fetal deaths/conceptions
because of the measurement error in the variable conceptions (i.e. live
births + fetal deaths). Such measure of conceptions would exclude all fetal
deaths before 28 weeks of gestation, which could be affected more by the
impact of non-economic damages cap leading to attenuation in the
estimated effect of the reforms.9
The
results
are
robust
to
using
all
fetal
deaths
occurring
after24 weeks of gestation. Results not reported but available on request.
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stay in effect and, thus, the incentives to choose a state
with caps over one without.
The estimates reported in column 3 of Table 2 are also
consistent with previous literature (Currie and MacLeod,
2008) and indicate that during the 19892001 period there
was a positive, significant correlation between non-
economic damages caps and the prevalence of C-sections
among
live
births.
The
estimated
effect
is
small,
a0.412 increase in C-sections per 100 live births, the
equivalent of a 2% increase calculated at the mean10. In
addition, during that period non-economic damages caps
were associated with 0.102 more prenatal visits for the
average women, the equivalent of a 0.9% increase.
There is a lag between the year of adoption and any
significant change in medical practice, providing reassur-
ance that the causality runs from the legislation to the
likelihood of surgical intervention during birth and not the
other way around11. When investigating the effect of this
reform on procedures over the entire 19892010 period,
however, neither the estimated effect on prenatal visits nor
that
on
C-sections
is
significant.
Two
standard
deviationsaround the estimated effect on prenatal visits before
2002 excludes the estimated effect over the 20022010
period, and in fact the estimated effects are of different
signs. The difference between estimates appears to be
much smaller in the case of C-sections, although the
0.254 estimated coefficient is the equivalent of 0.9%
increase in C-sections, half the effect over the pre-2002
period, and statistically insignificant. The lack of statistical
significance is not driven by larger standard errors but by
the smaller coefficient12. The smaller, insignificant effect of
newer reforms leads to smaller and insignificant estimates
on the pooled sample as well.
5.1.2. Buyers response
The second question is whether such supply changes
elicited any demand response that could have led to
changes in procedures. Do women respond to changes in
medical practice? A noisy way to address this question is to
look at the number of births. Women residing close to a
state border could respond by choosing a physician in the
border state. This measure is noisy because it is unlikely
pregnant women are very mobile and because our data
retain only live births, which contain a supply component:
the quality of care. When non-economic damages caps
affect the quality of care and thus are correlated with the
likelihood of survival in utero, the information contained in
the number of live births captures both a demand response
and a supply response. The results reported in Table 3
indicate noeffecton live births per 100 women of fertile age.
A better way to investigate this hypothesis is to look at
the initiation of an episode of care. While suppliers,
physicians, may decide the course of treatment, they can
only
do
so
if
women
initiate
an
episode
of
care.
Thus,
thetiming of prenatal-care initiation represents a cleaner
source of information about how women respond to
changes in medical practice. I find that non-economic
damages caps reforms passed during the 19892001
period were associated with earlier prenatal-care initia-
tion. This is consistent with previous literature indicating
that some of the savings experienced by physicians in
states with caps are passed to consumers: damage caps
increase health insurance coverage (Avraham and Schan-
zenbach, 2010).
These results are also not robust on the more
comprehensive sample and in fact change signs. Although
the
hypothesis
that
these
results
are
driven
by
measure-ment error in the dependent variables due to birth
certificates revision cannot be completely rejected, it does
not seem to pose a significant problem. The exclusion of
the control variable for revised data alters neither the sign
nor significance of the coefficients. In addition, the results
are consistent with those obtained on the sample of states
that did not implement revised birth certificates.
5.2. Falsification tests
5.2.1. Effect on outcomes
One way to investigate the plausibility of the results is
to
check
whether
other
variables
related
to
the
supply
ofmedical care changed in the same manner.
Table 4 reports the effect of non-economic damages
caps on a variety of birth outcomes. Interestingly, these
changes are associated with better health outcomes.
Between 1989 and 2001, non-economic damage caps are
associated with fewer births with low Apgar scores and
fewer instances of neonatal mortality due to injury.
Although there is a positive correlation between non-
economic damages caps and neonatal mortality due to
adverse effects of medical care, this association is not
significant at conventional significance levels13.
These effects, however, are not robust to using the more
comprehensive
sample,
which
is
fully
consistent
withprevious results indicating that the newer reform have less
bite.10 Currie and MacLeod (2008) found a 5% increase in the probability of C-
section, but they retain multiple births, while this paper does not, for
reasons explained in the data section. The C-section rate is higher among
multiple births.11 The estimated contemporaneous effect on ob-gyn is 0.031 with
standard error 0.022 and not statistically significant. The contemporane-
ous effect on C-sections is 0.267 with a standard error of 0.138 and, thus,
smaller and significant only at 10%. The lead policy variable is not
statistically significant.12 It is also not true that the lack of significance is driven by a longer lag
between the adoption and the response, such as may be expected if
people wait to see whether the reform will stick or be reversed. An event
analysis performed on the 20022010 data indicates statistically
insignificant
effects
at
all
lags;
results
reported
in
Appendix
Table
A2,available on request.
13 I find no evidence of a statistically significant change in the
prevalence of low birth weight, high birth weight, or in the average
birth weight. There is some evidence that during the 19892001 period
caps were associated with an increase in births at 39 weeks of gestation
and a decrease in those at more than 41 weeks of gestation. These results
are more suggestive of scheduled C-sections than of decisions taken at the
time of delivery and thus do not provide evidence that changes in health
drive the change in procedures. In addition, I find no evidence of a
statistically significant effect on induction over the entire sample or
within groups defined by gestation, which would suggest that a vaginal
delivery
was
attempted.
These
results
are
not
reported
but
are
availableon request.
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There are two possible explanations for these results.
One is a demand-based explanation. For instance, women
that care more about their health are more likely to be
aware of their health risks and, thus, start prenatal care
earlier and have better outcomes than women diagnosed
later during pregnancy. If these women with high-risk
pregnancies that warrant surgical intervention are more
mobile in their search for the right physician, non-
economic damages caps could be associated with more
C-sections and better outcomes. This explanation has
significant caveats. These women may be reluctant to
travel too far. Expecting to need more care, they could also
be
more
likely
to
avoid
a
state
with
a
decreased
cost
ofmalpractice even when the price of care is lower.
Alternatively, women that care more about their health
and have healthier births but also request surgical
intervention may be more mobile. In both situations, the
births in states with caps could be significantly different
from those occurring in the non-cap states. I follow Currie
and MacLeod (2008) to define high-risk women as those
suffering from following conditions: anemia, cardiac, or
lung conditions, diabetes, herpes, eclampsia, or incompe-
tent cervix, previous large or preterm deliveries, renal
failure, rh problems, uterine bleeding, or other risk factors.
Between 1989 and 2001 I find no evidence of a significant
change in the proportion of births to high-risk women
(coefficient
2.984
with
standard
error
of
1.865).
It
is
moredifficult to test the hypothesis that women that care more
Table 4
The impact of non-economic damages caps on birth outcomes.
Dep. Var. Premature births [1] 5 min Apgar
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about their health are more mobile. The increase in the
proportion of women that delay prenatal care reported in
Table 3 could be consistent with this hypothesis. However,
the
lack
of
a
significant
change
in
the
number
of
births
instates with caps, also reported in Table 3, seems more
suggestive of a response to lower prices, than of a selection
story.
A more fruitful area of investigation is a supply-based
explanation. The gains from easier access to specialized
medicalcare, ob-gyn,more than offsetany cost associated
with the risk of injury during surgical intervention, thus
leading to better overall outcomes. This explanation is
plausible. Evenwhen newentrants have lower diagnostic
skills and, thus, are both more prone to intervene
surgically (Currie and MacLeod, 2013) and more prone
to errors, the increase in competition may ensure that
only the most error-free physicians can maintain asuccessful practice. Thus, the risk of iatrogenic injury
might be small. The results regardingthe effect of caps on
mortality frommedical care adverse effects provide some
support for this proposed explanation.
Thehypothesis that the results are driven by selection
could also explain why none of the results obtained from
the 19892001 data can be replicated with the extended
19892010 sample14. In the following, I concentrate on
testing the supply-based explanation using the sample of
reforms passed before 2002, when the reforms are known
to be binding and produce an effect in the total
population. For instance, thepositivecorrelation between
caps and C-sections could be explained by increased risk
taking
by ob-gyns or
by a
change in
the
characteristics ofob-gyns due to selection. To separate one explanation
from the other I present results from a series of
falsification tests that show that most of the effect on
procedures is concentrated in areas with higher entry,
with little to no effect in areaswhere the structure of ob-
gyn population remained substantially the same, sugges-
tive of selection effects.
5.2.2. Effect by age of physicians
The hypothesis that the effect is driven by selection
relies on the assumption that the ob-gyn entrants are
different from the incumbents. Due to data availability, I
cannot
test
directly
whether
their
practice
style
isdifferent. However, because practice style is built through
education and experience, significant changes in the
demographics of ob-gyns provide indirect evidence of
differences in practice style. I find evidence of a statistically
significant increase in the number of ob-gyns under
35 years old in states that adopted caps before 2002
(see Table 5). The adoption of caps is associated with a
0.011 increase in ob-gyn per 10,000 women, the equivalent
of a 10% increase calculated at the mean of the data. There
is also some weak evidence, significant at the 10%
significance level, of an increase in the number of
physicians 6574 years old. Although quite noisy the
estimate
is
large.
It
represents
an
almost
10%
increase,
asignificant change if we are to compare it with the
estimated effect on physicians age 35 to 44, the equivalent
of a 2% increase.
These findings are consistent with previous literature
(Baicker and Chandra, 2005) and plausible, because young
ob-gyns at the beginning of their career are more mobile.
Once physicians have established their practices, which
often rely on referrals, changing their locationwould bevery
costly. At the same time, the prospect of lower practice costs
may induce some ob-gyns to defer retirement.
5.2.3. Effect by rurality
According
to
the
2003
Socioeconomic
Survey
ofAmerican College of Obstetricians and Gynecologists
Table 5
the impact of non-economic damages cap on the supply of Ob-Gyn by age of the physician.
Under 35 3544 4554 5564 6574 over 75
Panel A: 19952001
NE Cap 0.011** (0.005) 0.003 (0.004) 0.004 (0.005) 0.002 (0.003) 0.004* (0.002) 0.001 (0.002)
Obs. 17,695 17,695 17,695 17,695 17,695 17,695
Panel B: 19952010
NE
Cap
0.004*
(0.002)
0.003
(0.004)
0.004
(0.003)
0.000
(0.003)
0.002
(0.001)
0.000
(0.001)Obs. 40,047 40,047 40,047 40,047 40,047 40,047
Panel C: 20022010
NE Cap 0.002 (0.002) 0.003 (0.002) 0.001 (0.002) 0.000 (0.003) 0.001 (0.002) 0.001 (0.001)
Obs. 22,352 22,352 22,352 22,352 22,352 22,352
The dependent variables are the number of ob-gyn per 10,000 women by age of physician as noted in the heading of each column. The model specification
used for these regressions is identical to the one used in regressions reported in Table 2 column 1.
* Significant at 10% significance level.
** Significant at 5% significance level.*** Significant at 1% significance level.
14
Another
explanation
is
that
the
most
recent
reforms
are
not
binding.However, there is no evidence in support of that theory as the magnitude
of the cap is similar over time. Yet another explanation is repeals have
adoptions do not have symmetric effects. A large share of the variance in
the pre-2001 period is repeals whereas only 1 of the changes in the
2002 to 2010 period is a repeal. However, previous literature found there
is no difference between the effect of adoptions and repeals in the case of
medical procedures (Cotet, 2012). There is one paper that reports a
difference. Yoon (2001) found that the amount that plaintiffs recovered
fell by $23,000 in the period following the enactment of damage caps in
Alabama relative to the control states; while following the repeal of the
damage cap, the amount that plaintiffs recovered increased by $48,000
relative to the levels in the control states, However, two unusually high
payouts in the post-repeal period accounted for that asymmetry: after
omitting those cases, the decrease after repeal was found to be about
$20,000, an amount in line with the increase after enactment (Elliott,
2004).
There
is,
thus,
no
reason
to
believe
that
adoptions
and
repeals
haveasymmetric effects.
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(ACOG) Fellows, the vast majority of ob-gyns, 88%, practice
in metropolitan areas. This number did not change
between 1991 and 2003. This is quite plausible, given
the nature of the demand for their services and the
infrastructure used in the production of these services.
Natality data indicate that 98% of births took place in a
hospital. At the same time, ARF data indicate that
approximately 10% of counties had no hospital and another
40% had only one hospital. In fact, over the period
investigated,
80%
of
counties
had
a
maximum
of
twohospitals. Because deliveries take place in hospitals, ob-
gyns have to locate close to hospitals, which, as the data
indicate, tend to be located in metropolitan areas and other
urban areas. New entrants would also look for a location
reasonably close to a hospital. It is likely that there is more
entry into this field in metropolitan/urban areas. If our
results are driven by changes in the characteristics of the
body of ob-gyns practicing in an area, as opposed to a
change in the incentives of existing ob-gyns, we should
also observe larger changes in procedures and outcomes in
metropolitan/urban areas.
To test this hypothesis, I use the ARF 1995 classification
of
counties
rurality
and
define
urban
as
including
allcounties in metropolitan areas regardless of population
and counties with an urban population of 20,000 or more
adjacent to a metropolitan area. For the sake of brevity, I
report only the regressions for those outcome variables
previously found to be significantly affected by non-
economic damages caps. For all other variables, the effect is
not significant on either the urban or the rural sub-
sample15. The results reported in Table 6 are consistent
with the theory delineated above. Two standard deviations
around the effect on prenatal care initiation, or Apgar
scores estimated for urban counties exclude the effect in
rural areas. One standard deviation around the effect on
ob-gyns, C-sections or neonatal injury mortality in urban
areas excludes the effect estimated for rural areas.
5.2.4. Effect by number of hospitals
Although, ob-gyns prefer metropolitan locations, the
choice of location also depends on the demand for their
services. Matsa (2007) finds that the supply of physicians
increases more in relatively underserved areas16. There are
thus
two
margins
of
choice:
infrastructure
availability,
i.e.hospitals, and the demand for ob-gyn services. The
availability of hospitals captures the existence of infra-
structure that could be used for obstetric services. It
represents a measure of desirability of an area from a
professional point of view. It also captures the availabil-
ity of location options for an ob-gyn, thus being a
measure of desirability from a personal point of view. If a
county only has only one hospital then location options
are very limited because the ob-gyn likely cannot locate
too far from the hospital. This implies that ob-gyns may
locate in areas with at least one hospital but that are
relatively underprovided. To test this hypothesis, in
Table 7, I
split
the sample
by the
number of
hospitals
per10,000 people. Most of the effect is concentrated in areas
with a low number of hospitals per capita, with some
effect on prenatal initiation but no effect on outcomes in
areas with no hospitals or with many hospitals. This is
credible because even women in areas without a
significant influx of ob-gyns might benefit from lower
prices and, thus, they may be more likely to initiate care
Table 6
The impact of non-economic damages capseffect in rural versus urban areas.
Panel A. Supply
Ob/Gyn Prenatal visits Cesarean
All
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Table 8
The impact of non-economic damages caps by Lag ObGyn density.
Panel A. Supply
Ob/Gyn Prenatal visits Cesarean
All
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12/13
earlier, perhaps with a primary physician or general
practitioner. These results provide further support for
the hypothesis that the estimated effect of non-
economic damages caps is driven mostly by entry rather
than by changes in the practice style of existing
physicians.
5.2.5.
Effect
by
lag
ob-gyn
per
10,000
womenAnother measure of an areas suitability for new
entrants is the number of ob-gyn in previous period. A
low number of ob-gyn per women signals under-provision,
but the survival of any ob-gyn practices signals the
existence of basic infrastructure. The results reported in
Table 8 support the theory that before 2002 entry took
place mostly in areas relatively underserved, albeit not in
areas with most problems. The effect on procedures,
prenatal visits and C-sections, is also larger in the same
areas.
Of more interest perhaps is the effect of caps on health
outcomes, Apgar scores and neonatal mortality, which
seems
to
be
concentrated
in
areas
with
significantconcentrations of ob-gyn. These results match the results
regarding prenatal care initiation. In areas with high initial
concentrations of ob-gyn caps are associated with fewer
women delaying prenatal care initiation until the third
trimester. Thus, it could be that the effect on outcomes is
mostly due to the demand response to caps.
All this evidence is consistent with relatively small
changes in the practice style of incumbent ob-gyns and
larger changes in the overall practice style of ob-gyns in
states with caps due to entry. Thus, failure to account for
this source of variation would bias the estimate of ob-gyns
response to financial incentives. The overall conclusion is
that
the
lack
of
robustness
of
the
effect
of
non-economicdamages caps over time is likely driven by weaker supply
responses, either because of the signal contained in the
numerous repeals of caps or due to the reduced scope of
mobility.
6. Discussion and conclusions
Empirical results suggest that during the 19892001
period, non-economic damages caps reforms were associ-
ated with an increase in the number of ob-gyns, increases
in the number of prenatal visits and the rate of C-sections,
and better birth outcomes. The results are not robust to
the
addition
of
more
recent
reforms
taking
place
during
the20022010 period, however. This paper investigates the
role of selection among new entrants in explaining these
inconsistencies. It also provides some guidance toward
understanding the inconsistencies found in the literature
between the estimated effect of malpractice premiums on
procedures and that of non-economic damages caps that
reduce malpractice premiums on procedures.
First, the results reported in this paper suggest that the
earlier laws implementing caps on non-economic
damages produced changes in procedures and outcomes
in areas with more entry. In these areas, the demographic
structure of ob-gyns changed toward more young
physicians,
suggestive
of
changes
in
the
average
practicestyle through selection. Thus, non-economic damages
caps likely affected the market for obstetric services
through changes in access, changes in the incentives of
ob-gyns, and changes in the characteristics of service
provided by the average ob-gyn due to selection among
ob-gyns.
Failure to account for all these margins of choice
threatens the external validity of the estimated effect of
this
policy
on
physicians
behavior,
and,
thus,
extrapola-tion from state- to federal-level policies may not be
appropriate. When a sizeable part of the effect of the policy
is driven by young physicians location choices, the
estimated coefficients overestimate the impact of changes
in the incentives faced by the average ob-gyn.
Second, the evidence presented in this paper suggests
that although earlier non-economic damages caps reforms
led to changes in medical practice that mirror the effect of
higher malpractice premiums (i.e., they are positively
associated with higher C-sections rates and more care),
the results need not be inconsistent with each other. Rather,
the correlation between malpractice premiums and proce-
dures
reflects
incentive effects,
while
the
associationbetween non-economic damages caps and procedures
reflects selection effects that could obscure the effect of
changes in incentives. Because malpractice premiums were
found to lead to more C-sections (Dubay et al., 1999; Grant
and McInnes, 2004) while non-economic damages caps
were found to act mostly though selection, it is more
plausible that in general, C-sections are not a sign of risk-
taking among ob-gyns.
In addition, the results are consistent with the idea that
non-economic damages caps lead to changes in outcomes
through increased pressure of competition. Both the lower
cost of malpractice and the shift in supply toward
physicians
with
less
experience
would
suggest
greaterpotential for medical errors. The results do not completely
reject the hypothesis that non-economic damages caps
increase medical errors, because although the estimated
effect on infant mortality from medical care adverse effects
is not statistically significant, it is positive and economi-
cally significant. The implied effect, albeit very imprecisely
estimated, is more than 30% increase in infant mortality
due to adverse effects from medical care. Increased
competition, however, can offset some of this increase in
medical errors by easing access and putting pressure on
physicians to perform, thus, leading to a net positive effect
on outcomes, as identified in this paper.
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Further
reading
National Center for Health Statistics, 1999. Bridged-race IntercensalEstimates of the July 1, 1990July 1, 1999, United States ResidentPopulation by County, Single-Year of Age, Sex, Race, and HispanicOrigin, Prepared by the U.S. Census Bureau with Support from theNational Cancer Institute. National Center for Health Statistics Avail-able on the internet athttp://www.cdc.gov/nchs/nvss/bridged_race.htm.
National Center for Health Statistics, 2010. Postcensal estimates of theresident population of the United States for July 1, 2000-July 1, 2010,by year, county, single-year of age (0, 1, 2,. . ., 85 years and over),bridged race, Hispanic origin, and sex (Vintage 2010). Prepared Undera Collaborative Arrangement with the U.S. Census Bureau. NationalCenter for Health Statistics Available fromhttp://www.cdc.gov/nchs/nvss/bridged_race.htm.
A. Cotet-Grecu /Economics and Human Biology 17 (2015) 2941 41
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