Module 2 discussion-

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Journal of Health Economics 60 (2018) 75–89

Contents lists available at ScienceDirect

Journal of Health Economics

jo ur nal homep age: www.elsev ier .com/ lo cate /econbase

ffects of Medicare coverage for the chronically ill on health
nsurance, utilization, and mortality: Evidence from coverage
xpansions affecting people with end-stage renal disease�

artin S. Andersen
epartment of Economics, UNC Greensboro, 516 Stirling Street, Greensboro, NC 27412, USA

r t i c l e i n f o

rticle history:
eceived 21 June 2017
eceived in revised form 1 June 2018
ccepted 4 June 2018
vailable online 18 June 2018

EL classification:
13
18
51

a b s t r a c t

I study the effect of the 1973 expansions of Medicare coverage among individuals with end-stage renal
disease (ESRD) on insurance coverage, health care utilization, and mortality. I find that the expansions
increased insurance coverage by between 22 and 30 percentage points, in models that include trends in
age, with the increase explained by Medicare coverage, and increased physician visits by 25–35 percent.
These expansions also decreased mortality due to kidney disease in the under 65 population by between
0.5 and 1.0 deaths per 100,000. Lastly, I provide evidence for two mechanisms that affected mortality:
an increase in access to and use of treatment, which may be due to changes in insurance coverage; and
an increase in entry of dialysis clinics and transplant programs.

© 2018 Elsevier B.V. All rights reserved.

eywords:
nsurance

ortality
idney disease
ealth

ealth insurance

. Introduction

The United States has typically expanded public insurance pro-
rams by providing coverage to distinct demographic groups. For
xample, the introduction of Medicare and Medicaid in 1966 pro-
ided insurance coverage to people who were 65 and older or had
ow income. However, several expansions of these programs have
efined eligibility based in part on the presence of medical condi-
ions (e.g. long-term disabled, people with end-stage renal disease,
regnant women, and women diagnosed with breast or cervical

ancer). By selecting on ill-health, the effects of a disease-specific
nsurance expansion on insurance coverage, health care utilization,

� Aaron Ladd, James Frizzell, and Mohamad Noureddine provided excellent
esearch assistance. Dr. Glenn Gee provided helpful insight into the coding and epi-
emiology of kidney disease. I thank the Editor, Kitt Carpenter, three anonymous
eferees, and participants at the UNCG Brown Bag, the NBER Health Economics pro-
ram meeting, and the Southern Economic Association, American Society of Health
conomists, AEA/ASSA Annual Meetings for helpful comments. As usual, any errors
nd omissions are my own.

E-mail address: [email protected]

ttps://doi.org/10.1016/j.jhealeco.2018.06.002
167-6296/© 2018 Elsevier B.V. All rights reserved.

and health outcomes may differ considerably from the effects of
more broad-based expansions.

Previous studies of the Medicare and Medicaid programs have
demonstrated that Medicare may reduce mortality (Card et al.,
2009; Chay et al., 2017), increase health care utilization (Card
et al., 2008), and improve financial risk protection (Barcellos and
Jacobson, 2015; Engelhardt and Gruber, 2011), while the intro-
duction of state Medicaid programs reduced infant mortality
(Goodman-Bacon, 2017). More recent evidence from an expansion
of Medicaid for pregnant women demonstrates improvements in
infant health outcomes (Currie and Gruber, 1996) and a related
expansion affecting children improved their health and increased
health care utilization (Currie and Gruber, 1996). A recent ran-
domized study of the Oregon Medicaid program (Finkelstein et al.,
2012) also demonstrated greater health care utilization and better
self-rated physical and mental health among people randomized
to receive Medicaid coverage, although there was no statistically
significant difference in mortality.

There is, to my knowledge, no empirical evidence of the effects

of three other disease-specific insurance expansions that provided
insurance coverage for women with breast or cervical cancer,
the long-term disabled, and people with end-stage renal disease

7 ealth E

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6 M.S. Andersen / Journal of H

ESRD). In this paper, I examine the effect of a 1973 Medicare expan-
ion that provided coverage to two groups of people: long-term
eneficiaries of the Social Security Disability Insurance (SSDI) pro-
ram and people who are undergoing dialysis or have received a
idney transplant due to having end-stage renal disease. The focus
f this paper is the effect of the expansion on people with kidney
isease who became eligible for Medicare coverage through either
he ESRD route, if they were not already receiving SSDI payments, or
ue to SSDI receipt. Consistent with prior practice of the Medicare
rogram itself, I consider both sets of enrollees as being enrolled in
he ESRD program.1

These expansions are attractive to study for several reasons.
irst, the introduction of the program was, for the most part, unan-
icipated so that there is unlikely to be any significant anticipatory
ffects (Ball, 1973). Second, people with kidney disease tend to be
n extremely poor health, so insurance is likely to have unusually
arge effects on health. Third, because for most people treatment

as unaffordable prior to the expansion and insurance typically did
ot cover treatment (Rettig, 2011; Congressional Research Service,
971), these results provide some insight into the welfare conse-
uences of moral hazard induced spending since the bulk of any

ncrease in utilization can be attributed to ex-post moral hazard.
he ESRD program is also worthy of study on the basis of the size
f the program. In 2015 the United States spent over $30 billion
o treat 500,000 Medicare beneficiaries with ESRD, which repre-
ents 1% of all Medicare beneficiaries and 5% of Medicare spending.
n other words, the ESRD program is almost as large as the entire

edicaid program in the state of Texas, which is the third largest
edicaid program (by spending) in the country.
In order to identify the effect of the ESRD program, I estimate

riple-difference models that compare outcomes for people over
5, who were always eligible for Medicare coverage, versus those
nder 65, before versus after the expansion took effect, with versus
ithout ESRD. However, due to the expansion of Medicare coverage

o the long-term disabled, the triple difference estimate is biased.
ence, I also estimate difference-in-differences models that con-
ition on having ESRD, which yields unbiased estimates as long as
here is no selection into treatment, i.e. as long as ex-ante moral
azard is small. These two estimators will yield similar results as

ong as either the effect of Medicare eligibility is small in the non-
SRD group or the share of people eligible for Medicare coverage
n that group is small.

In this paper I document three main facts about the ESRD pro-
ram. First, I demonstrate that the ESRD expansion significantly
ncreased insurance coverage among people under 65 years of
ge with kidney disease. Close to the traditional Medicare eligi-
ility threshold of 65, I find a 22.6–29.6 percentage point increase

n the probability of any insurance coverage among people with
idney disease. I find somewhat larger increases in Medicare cover-
ge (26.0 and 33.9 percentage points, respectively), indicating that
ome people would have had insurance coverage in the absence of
he expansion.

Second, I find that the ESRD expansion increased physician visits
y 25–35 percent for people with kidney disease below 65 years of
ge. The increase in physician visits is consistent with my results on
ealth insurance coverage and implies that a 10 percent increase

n the share of the population with insurance increases physician

isits by about eight percent. Because of the wording of the survey
uestion that I use to assess physician visits, it is also possible that

1 The Medicare Trustees’ Reports from this period all pool the ESRD population
nd the disabled with ESRD populations because the disabled population with ESRD
s more similar to the non-disabled ESRD population than the rest of the disabled
opulation.

conomics 60 (2018) 75–89

the increase in physician visits represents an increase in visits to,
among other things, dialysis clinics.

Third, I document a significant reduction in mortality due to
kidney disease of between two and seven log points, depending on
specification and definition of kidney disease. I am able to replicate
this finding in cross-national comparisons as well that allow me to
control for innovations in kidney disease treatment across coun-
tries. My results imply that the program averted between 174 and
325 deaths per year for whites between 45 and 64 years of age (my
estimation sample). Assuming that the entire change in mortality
arose among people who gained insurance coverage, then my mor-
tality and insurance results imply that the probability of dying in
the coming year of kidney disease fell by 0.2–0.5 percentage points.

I am also able to provide evidence in support of two mech-
anisms by which the ESRD expansion affected health. First, the
state-specific effect of the ESRD expansion on kidney disease mor-
tality was larger in states that had more treatment facilities per
capita in 1971. One interpretation of this result is that the presence
of treatment facilities reduced mortality by increasing access to
treatment. This interpretation is also consistent with the increase
in physician visits. Second, I document an increase in the number
of dialysis clinics and transplant programs per capita from 1971
to 1975 in states that had a higher under 65 mortality rate due
to kidney disease, which is consistent with a demand side shock
encouraging entry of new treatment facilities.

My mortality estimates also allow me to extrapolate to changes
in survival and imply that the expansion saved between 2000
and 14000 life years, based on the change in survival for 45 year
olds. This range encompasses some values where, using a value of
$100,000 per statistical life year, the cost of the program are out-
weighed by the survival benefits. However, these estimates ignore
other costs that the program imposes on society (e.g. increased dis-
ability insurance payments) but also ignores the value of spillover
effects on to people 65 and older.

The remainder of the paper proceeds as follows. Section 2 pro-
vides background information on end-stage renal disease, discusses
the role that the federal government has played in the treatment
of ESRD, and describes the 1973 Medicare expansions that I study.
Sections 3 describes the data that I use for my analyses and the
empirical approach that I take, while |Sections 4 present my main
results from the Medicare expansion in 1973. Section 5 presents
potential mechanisms behind my results. Section 6 discusses the
welfare implications of my results. Section 7 concludes.

2. Background

End-stage renal disease (ESRD) is the end result of a progressive
decline in kidney function due to chronic kidney disease. Leading
causes of ESRD and chronic kidney disease include chronic kidney
disease include diabetes, hypertension, glomerulonephritis, poly-
cystic kidney disease, kidney stones, urinary tract infections, and
various congenital defects (National Kidney Foundation, 2009).2

The loss of kidney function that characterizes ESRD leads to a rapid
buildup in toxins and disregulation of potassium and sodium levels
in the blood that, left unchecked, rapidly leads to death.

Treatment for ESRD emphasizes restoring or augmenting the
body’s ability to filter out toxins and maintaining electrolyte levels

either by transplanting a functioning kidney from either a living
or cadaveric donor or by externally filtering blood using a dial-
ysis machine. There were significant scientific advances affecting

2 Appendix Table A lists the ICDA-8 codes that I use to identify deaths with these
underlying cause of death codes. In analyses using the National Health Interview
Survey, I also include data that uses ICD-7 and ICD-9 codes, which are also identified
in the appendix table.

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they were not eligible for the ESRD program.
I code each death as being a kidney disease death, or not, based

on either the underlying cause of death, which the World Health

M.S. Andersen / Journal of H

oth forms of treatment in the late 1950s through the 1960s. The
rst successful kidney transplant was performed in 1956 with the
ubsequent decade leading to slow, but steady, improvements in
ransplantation (Congressional Research Service, 1971) so that by
971 there were 1172 kidney transplants performed (Rettig, 1976).
hroughout this period, kidney transplantation was a costly proce-
ure with the Congressional Research Service (1971) estimated that
idney transplantation had a nominal one-time cost of $10,000 to
20,000 ($59,000 to $117,000 in 2015) and maintenance costs of
1,000 per year ($5,900 in 2015).

Chronic dialysis, which is what is necessary to treat ESRD, was
ot feasible until 1960. Furthermore, at its inception, dialysis was
xtremely costly leading to rationing at the first dialysis clinic in
he United States (Alexander, 1962). In July of 1972, there were
786 living dialysis patients in the United States (Rettig, 1976, p.
00) and the Congressional Research Service (1971) estimated that
he annual cost of dialysis was $15,000 in 1971 (nominal dollars,
85,000 in 2015 using the CPI-U).

Despite the availability of treatment modalities in the late
960s and early 1970s, the Congressional Research Service (1971)
eported that most health insurance plans did not cover treatment
or ESRD.

During the 1960s, the federal government took an active role in
romoting the diffusion of treatments for ESRD as well as funding
esearch and development of new treatments. In 1963, the Vet-
ran’s Administration began to open dialysis clinics in its hospitals
cross the country and, by 1971, there were 40 dialysis facilities and
5 transplant programs open at VA and military hospitals across
he U.S. Beginning in 1964, the National Institutes of Health started
rograms to study transplant immunology, which was intended to

ncrease the number of successful kidney transplants. In 1965, the
ublic Health Service started the Kidney Disease Control Program,
hich provided start-up grants to open a dozen dialysis centers

Rettig, 1991). The federal government, through the Bureau of the
udget, also began examining the fiscal implications of the growth

n ESRD and the advent of new methods to treat ESRD, although
hese discussions ultimately did not appear to have affected federal
olicy (for further discussion see Rettig, 1991).

In 1972 Congress, for the first time, passed a law expanding eli-
ibility for Medicare coverage, with the expansion taking effect on
uly 1, 1973. Congress did so by declaring that two groups were eli-
ible for coverage people who: had been eligible for Social Security
isability Insurance (SSDI) benefits for more than 24 months; or
ave received three, or more, months of renal dialysis with cover-
ge extending up to twelve months after a person received a kidney
ransplant.

Neither component of the expansion was truly universal since in
oth cases, only individuals who were eligible for insurance under
he Social Security program became eligible. Collectively, these two
rograms increased Medicare enrollment by 1.7 million people, of
hom 6,371 were eligible solely due to the ESRD in the first year of

he program. By 1978, there were almost 44,000 Medicare benefi-
iaries with ESRD, of whom almost 35,000 were under 65 years of
ge, with per capita spending of almost $65,000 (in 2015 dollars).

The ESRD component of the expansion (which includes long-
erm disabled with ESRD), which was initially expected to enroll
5,000 people and cost $1 billion (nominal) per year, rapidly bal-

ooned in size, covering more than 50,000 people and costing over
1 billion per year in 1979 (Table 1). In 2013, the ESRD program
overed almost half a million people at a cost of $30 billion, which
epresents approximately 1% of Medicare enrollees and 5% of Medi-
are spending.

conomics 60 (2018) 75–89 77

3. Data and empirical framework

3.1. Data

I use data from a variety of sources to measure insurance cov-
erage, health care utilization, and mortality in my main analyses as
well as data on potential mechanisms and confounding factors. In
this subsection, I describe each of these data sources.

3.1.1. Insurance coverage and health care utilization
The National Health Interview Survey asked respondents about

insurance coverage in even numbered years beginning in 1968,
although the specific wording and universe for various questions
has changed over time. In 1968 the NHIS inquired about health
insurance generically and did not differentiate between public and
private coverage and it was not until 1978 that the NHIS inquired
about Medicare coverage for people under 65 years of age. In the
1974 and 1976 waves of the survey individuals with only Medicare
coverage were instructed to respond that they were uninsured. As a
result, I present results using data from 1968, 1970, 1972, 1978, and
1980 for most insurance outcomes (I include data on private insur-
ance coverage in 1974 and 1976). I define an individual as having
private insurance coverage based on whether or not an individual
reported having private hospital coverage (as in Finkelstein, 2007)
and define Medicare coverage in a comparable manner.

The NHIS also included questions on the number of doctor vis-
its in the prior year beginning in 1969, which I use to measure
health care utilization. Because the NHIS questions refer to treat-
ment received over the prior year, I omit people 65 years of age from
the utilization analysis and all data from July 1973 through June
1974, the 12 months following the implementation of the Medicare
expansion.

I use the condition inventory and the list of conditions that
caused the interviewee to miss days from work or access health
care services to construct indicators for the presence of kidney dis-
ease. The coding is based on the codes for the broad definition,
but incorporating the NHIS omissions, listed in Appendix Table A.
In total, out of 371,181 people in the NHIS, I identified 1644 peo-
ple between 45 and 84 years of age with kidney disease using the
broad definition. Despite the small sample size, the ESRD expan-
sion is likely to have led to large changes in insurance coverage,
hence I remain sufficiently powered to identify effects of the ESRD
expansion on insurance coverage. For the utilization analyses, it is
possible that I will be underpowered to detect effects if the increase
in physician visits from the expansion is small.

3.1.2. Mortality
I use the Multiple Cause of Death files from the National Center

for Health Statistics’ (NCHS) for the years from 1968 through 1978
(United States Department of Health and Human Services, 2007,
2007). These data provide the state and county of residence, race,
gender, age, underlying cause of death and all other diagnoses listed
on the death certificate for all deaths in the United States, except in
1972, when the NCHS was only able to process half of the submit-
ted death certificates.3 Preliminary analyses of the distribution of
deaths by age indicated significant excess mass at five-year inter-
vals of age for non-white individuals, which was also reported in
Honoré and Lleras-Muney (2006), so I omit non-whites from my
mortality analyses. I also drop deaths to non-U.S. residents since

3 Since I use functions of the count of deaths in a given demographic-time cell as
my dependent variable, I multiply the count of deaths in 1972 by 2.

78 M.S. Andersen / Journal of Health Economics 60 (2018) 75–89

Table 1
Enrollment, spending, and utilization in the ESRD program.

Year Enrollment Kidney Deaths Spending Utilization

Total Under 65 Under 65 65 and Over Total Per enrollee Transplants Dialysis

1971 5335 7534
1974 15993 4633 8949 1050.3 65673
1975 22674 12702a 4540 9491 1545.6 68164
1976 28941 14721a 4532 10597 2086.9 72110
1977 35889 16514a 4345 11008 2449.2 68243
1978 43482 34828 4498 11973 2804.6 64500
1979 52636 43031 3761 11966 3126.4 59397 4189 45565
1981 61930 47520 3761 13703 3723.7 60127 4898 58924
1986 93197 59570 3914 17851 6786.7 63646 8948 90886
1991 142510 83443 3395 17963 9704.2 56844 10037 144175
1996 255578 3433 20869 14141.8 55333 12219 215557

Source—Greenbook (various years), Annual Statistical Supplement to the Social Security Bulletin (various years), Multiple Cause of Death files, 1971–1996.
a Enrollees eligible solely due to ESRD.

N edica
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otes—Enrollment based on enrollment in Medicare Part A, expenditures are for M
orkers. Utilization data are the number of transplants and number of enrollees dial

he coding of kidney deaths changed between 1978 and 1979.

rganization defines as “the disease or injury that initiated the train
f events leading directly to death, or the circumstances of the acci-
ent or violence which produced the fatal injury,” or using any of
he diagnosis codes listed on the death certificate. For each source
f cause of death diagnosis codes, I defined a death as due to kidney
isease using three sets of diagnosis codes. First, I defined a “nar-
ow” definition of kidney disease, which did not restrict to only
hronic disease, but is generally based on the “renal failure” codes
n the ICDA-8. Second, I created a “chronic” definition by restrict-
ng the narrow definition to deaths due to chronic causes. Lastly, I
reated a “broad” definition, which was based on the codes used by
he Kidney Disease Program in tracking kidney disease mortality
Kidney Disease Program, 1971). Appendix Table A lists the ICDA-8
iagnosis codes for the three cause of death groupings that I use.

I combine the mortality data with population data from the SEER
rogram and the U.S. Census Bureau in order to adjust for changes in
he size of the population over time, which also affects the expected
umber of deaths due to kidney disease. Because these data do not
reak out population figures for individuals 85 and over, I restrict
y analysis to deaths to individuals who are 84 or younger.

.1.3. Mechanisms and confounders
In my discussion of mechanisms and potential confounders,

elow, I rely on data from three other datasets. I collected data
n the geographic distribution of treatment facilities in 1971 from
he publication “Kidney disease services, facilities, and programs
n the United States” (Kidney Disease Program, 1971), which lists
reatment facilities by state. Based on the name of the facility, I also
lassified these facilities into Veteran’s Administration/Military vs.
ivilian categories since access to the former may be restricted. Data
n treatment facilities in 1975 came from the 1977 Annual Sta-
istical Supplement to the Social Security Bulletin, which lists the
umber of hospital transplant programs, hospital-based dialysis
linics, and free-standing dialysis clinics by state.

I collected data on the share of people in an age-gender-state
ell who receive income from either Social Security or the Supple-
ental Security Income program from the March CPS supplements

or 1977–1979 (spanning 1976–1978).

.2. Empirical approach

.2.1. Identification

My data includes three sources of variation that I could use to

dentify the effect of the Medicare ESRD program on insurance cov-
rage, health care utilization, and kidney disease mortality. First,
here are differences over time in Medicare eligibility for individu-

re Parts A and B. Spending data have been inflated to 2015 using the CPI for urban
respectively. Kidney deaths are based on chronic coding only, see Appendix Table A;

als of the same age and disease status. Second, there are differences
by age in eligibility for Medicare for individuals in the same year and
disease status. Third, there are differences by disease status in eligi-
bility for Medicare coverage for individuals in the same year and of
the same age. In principle, these three sources of variation would
justify a triple difference estimator assuming that potential out-
comes between these groups satisfy a “parallel trends” assumption
(Lee and Kang, 2006). However, in my setting the parallel trends
assumption is unlikely to hold because the SSDI expansion means
that there is partial takeup of Medicare coverage in one of the com-
parison groups. The structure of the problem, allows me to identify
the source of any bias from these comparisons and identify a solu-
tion that leads to unbiased estimates of the intent-to-treat effect of
the Medicare expansion on people with kidney disease.

To demonstrate the bias and identify situations in which it does
not affect my results, let Ye

akt
denote the potential outcome for

someone in age group a (a = 1 for people under 65) who has kidney
disease if k = 1, in time period t (t = 1 in the post period), and is either
eligible (e = 1) or ineligible (e = 0) for Medicare coverage. Assume
that there is a probability ˛akt that a person is eligible for Medicare
in each akt cell and define Yakt = ˛aktY

1
akt

+ (1 − ˛akt)Y0
akt

. Ignoring
the fact that some people 65 and older are not eligible for Medi-
care, Medicare program rules imply that ˛0kt = 1 for all k, t ∈ {0, 1}
and ˛1k0 = 0 for k ∈ {0, 1}. Finally, because (almost) everyone with
kidney disease is automatically eligible for Medicare coverage, but
only some people without kidney disease are eligible for Medicare
coverage, we also have ˛111 > ˛101.

Then the triple-difference estimator can be written as:

DDD = ˛111
(

Y1
111 − Y0

111

)
− ˛101

(
Y1

101 − Y0
101

)
+

[ (
Y0

111 − Y0
110

)
−

(
Y1

011 − Y1
010

)
−

(
Y0

101 − Y0
100

)
+

(
Y1

001 − Y1
000

)
]

The “parallel trends” assumption can be stated as the assumption
that the terms in the large brackets in the previous equality vanish
and that ˛101

(
Y1

101 − Y0
101

)
= 0. While it is plausible that the second

and third terms vanish, the ˛101
(

Y1
101 − Y0

101

)
, which reflects the

effect of the expansions on the disabled without ESRD, is unlikely
to vanish. Therefore DDD is biased by partial takeup of treatment
(˛111 < 1) and the fact that some people without kidney disease
are also treated (˛101 > 0). However, the bias can be signed if one
assumes that the sign of the treatment effect is the same regard-

less of kidney disease status, in which case the triple-difference
estimate will be biased towards zero unless the treatment effect of
eligibility for people without kidney disease is significantly greater
than the treatment for people with kidney disease.

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fact that the Medicare expansion’s effect on people without kidney
disease appears to bias my DDD estimates towards zero for having
any insurance coverage and for Medicare coverage. This bias is what

M.S. Andersen / Journal of H

In the difference-in-difference estimate that restricts to peo-
le with kidney disease, there is no bias from the fact that people
ithout kidney disease are partially treated. One can write this

stimator as:

Dk = ˛111
(

Y1
111 − Y0

111

)
+

(
Y0

111 − Y0
110

)
−

(
Y1

011 − Y1
010

)
ssuming that the parallel trends assumption holds, then DDk pro-
ides a scaled estimate of the causal effect of Medicare eligibility
or people with kidney disease. In the DDk estimator, the parallel
rends assumption implies that in the absence of the ESRD expan-
ion, trends in mortality would have progressed along similar paths
ollowing the expansion for people over and under 65 years of
ge. While there are reasons to doubt this assumption, due to the
act that renal replacement therapy was generally more suited to
ounger, rather than older, people, it is unclear why there would
e a sudden change at age 65, as would be required to bias my
stimates.

It is tempting to also consider difference-in-difference models
hat compare people with and without kidney disease who are
nder 65, but such a model would be subject to the same biases
s the triple difference model since some people without kidney
isease also became eligible for Medicare coverage following the
973 expansions.

.2.2. Event study and difference-in-difference models
I first consider analyses that use age and time variation sepa-

ately. To do so, I estimate event-study models of the form:

yiatgd = ˇ65
1 Kidneyd + ˇ65

2 Postt + ˇ65
3 Kidneyd × Postt

+
∑

a′ /= 65

(ˇa′
1 Kidneyd + ˇa′

2 Postt + ˇa′
3 Kidneyd × Postt)1[a=a′]

+Xig�1 + �t + ˛a + ε

(1

nd

yiatgd = ˇ1971
1 Kidneyd + ˇ1971

2 Under65a + ˇ1971
3 Kidneyd × Under65a

+
∑

t′ /= 1971

(
ˇt′

1 Kidneyd + ˇt′
2 Under65a + ˇt′

3 Kidneyd × Under65a

)
1[t=t′]

+Xig�1 + �t + ˛a + ε

(2a)

here yiatgd is the outcome—type of insurance coverage, amount of
ealth care utilization, or deaths per 100,000 people—for person i (I
nly have person-level data on insurance coverage), who belongs to
ge group a in time period t, where time is measured in half-year
ncrements (although there is some abuse of notation), gender g,
nd cause of death d, Kidneyd is a dummy for deaths due to kidney
isease, Postt is a dummy for the ESRD period, which takes the value
f 1 for time periods after July 1, 1973, Under65a is an indicator that

is less than 65, Xig is a vector of controls including fixed effects for
ach demographic group, �t and �a are year and age fixed effects,
espectively. The coefficients ˇa

i
and ˇt

i
are the age or year-specific

oefficients on kidney disease, the post period (or being under 65),
nd their interaction.

I then summarize the results of these event studies using a
riple-difference estimator, which is subject to bias from the SSDI
rogram, and a difference-in-differences estimator that is unbi-
sed, but may also be less precise. The triple-difference model can
e written as:

yiatgd = ˇ1Kidneyd + ˇ2Postt + ˇ3Under65a + ˇ4Kidneyd × Postt

+ˇ5Kidneyd × Under65a + ˇ6Postt × Under65a (3

+ˇ7Kidneyd × Postt × Under65a + Xig�1 + �t + ˛a + ε

nd the corresponding difference-in-differences estimator is:

yiatgd = ˛1Postt + ˛2Under65a + ˛3Postt × Under65a + Xig�1 + �t + ˛a + ε (4)

conomics 60 (2018) 75–89 79

The previous discussion of identification in this setting implies that
|˛3| ≥ |ˇ7|, assuming that treatment effects in the ESRD expansion
are comparable in size, or larger, than treatment effects of the SSDI
expansion.

Standard errors for all models are clustered on age and time,
unless otherwise specified, using clus nway.ado (Kleinbaum et al.,
2013; Cameron et al., 2011). I cluster on age to be consistent with
the recommendations in Lee and Lemieux (2010) and Lee and Card
(2008). I cluster on time based on recent results in Hausman and
Rapson (2017).

4. Effect of the Medicare expansion

4.1. Health insurance

I first consider the effect of the Medicare expansion on health
insurance coverage among people with kidney disease. Fig. 1
presents an event study of the change in any insurance coverage
(panel A) and Medicare coverage (panel B) using the triple-
difference version of equation 1b.4 Prior to the Medicare expansion,
the probability that an individual with kidney disease had any form
of insurance coverage was increasing from 1968 to 1970, but sta-
ble from 1970 to 1972. However following the expansion there
was no appreciable increase in insurance coverage, on average,
for people with kidney disease. Medicare coverage, by contrast,
increased significantly by 1978 with the bulk of the increase in
Medicare coverage happening at older ages (panel D). Conversely,
the ESRD expansion appears to have increased coverage somewhat
for people close to the age 65 cutoff, but there was also a noticeable
increase in insurance coverage for people around 40 years of age
(panel C).

The results in Fig. 1 provides some support for the “parallel
trends” assumption underlying differences-in-differences estima-
tors. The fact that there was an increase in the point estimates
from 1968 to 1970 for the probability of having any insurance is
concerning, but this trend does not continue into 1972. I find no
indication of a time trend in Medicare coverage. By age, panels C
and D demonstrate that insurance coverage for people over 65 was
not appreciably affected by the Medicare expansion.

Consistent with the event study in Fig. 1, I find no evidence that
the ESRD expansion increased insurance coverage among people
with kidney disease (Table 2, column 1). However, there was a
23–30 percentage point increase in coverage for people close to
the age 65 cutoff (column 2). The increase in insurance coverage
in models with age trends is slightly smaller than the increase in
Medicare coverage (columns 3 and 4), which is consistent with
either a degree of crowd-out or “doubling-up” of private and pub-
lic insurance coverage. I find only modest evidence of a decrease
in private insurance coverage associated with the ESRD expansion,
but a large decrease in the share of people who reported only pri-
vate insurance coverage. This final change–the reduction in reports
of only private insurance–is indicative of people using both Medi-
care and private insurance coverage simultaneously. This kind of
doubling up of insurance coverage provided additional benefits to
people with ESRD since private insurance plans at the time typically
did not cover dialysis or renal transplantation, hence adding Medi-
care coverage represented a significant improvement in insurance
coverage for people with kidney disease.

Comparing the DDD and DD coefficients provides support for the

4 The figure using the difference-in-difference is similar, but less precisely esti-
mated.

80 M.S. Andersen / Journal of Health Economics 60 (2018) 75–89

Fig. 1. Changes in insurance coverage from the Medicare expansion. Source—National Health Interview Survey, even number years from 1968 to 1980, excluding 1974 and
1976. Notes—Sample in panels A and B restricted to people between 45 and 84 years of age; panels C and D use everyone between 18 and 84 years of age. Points in panels
A and B are year-by-under 65 years of age-by-kidney disease coefficients from a regression of insurance status on year fixed effects (omitted 1970), an under 65 indicator,
an indicator for kidney disease, and all two- and three-way interactions. Panels C and D present point estimates for years of age interacted with a post dummy (after 1973)
and kidney disease from regressions of insurance status on age fixed effects, post, kidney disease, and all two- and three-way interactions; smoothed line is local polynomial
e dash
i ile pa
u

o
a
b
d

e
t
p
t
o
a
i
r
p
o
s
a
p
e
r
b
d

stimate where estimates are weighted by the inverse of their standard errors and
ntervals in panels A and B based on covariance matrix that is clustered on age, wh
sing the “broad” definition (see appendix Table A).

ne would expect if the Medicare expansion also affected insur-
nce coverage for some people without kidney disease, in this case
y providing coverage to the long-term disabled without kidney
isease.

The row labeled “Agg. Effect” presents the average aggregate
ffect of the Medicare expansion on insurance coverage using the
riple difference or difference-in-difference coefficient, as appro-
riate. The average aggregate effect is the average of the annual
otal of the sampling weight for people between 45 and 64 years
f age with kidney disease multiplied by the DDD or DD coefficient
nd indicates how many people with kidney disease gained or lost
nsurance coverage as a result of the Medicare expansion. These
esults indicate that as few as 5400 people or as many as 58000
eople with kidney disease gained insurance coverage as a result
f the expansion, although only the higher estimate is based on a
tatistically significant coefficient. Using data on Medicare cover-
ge, I find a large increase in coverage of between 37000 and 66000
eople having Medicare coverage. My estimates for Medicare cov-
rage are large and are, in fact, larger than what Medicare trustees

eported for the total number of people with ESRD, whether they
ecame eligible solely due to having ESRD or because they were
isabled. The fact that my implied increase in Medicare coverage

ed lines are 95% confidence intervals of the local polynomial estimate. Confidence
nels C and D use heteroskedasticity robust standard errors. Kidney disease defined

is larger than the estimate from Medicare trustees should not be
surprising since, in order to have sufficient data, I am applying a
far more relaxed definition of kidney disease than is used by Medi-
care itself. The aggregate effect estimated using the DD coefficient
is consistently larger than the estimate from the DDD estimate,
which is what I had hypothesized based on the fact that some peo-
ple without kidney disease were also gaining access to Medicare
coverage.

As a specification check, online appendix Table B1 presents
results from “donut” regressions that exclude people within five
years of turning 65. These donut estimates are, in general, consis-
tent with my main specifications, particularly for models without
age trends.

4.2. Health care utilization

Fig. 2 presents triple difference estimates for the number of
physician visits. The estimates in panel A are extremely noisy, both

in terms of the standard error, but also in the point estimate itself,
with relatively large amount of variation in the point estimate both
before and after the expansion took effect. However, visually it
appears that there may have been an increase in physician visits

M.S. Andersen / Journal of Health Economics 60 (2018) 75–89 81

Table 2
Effect of the ESRD program on health insurance and health care utilization.

Any insurance Medicare Any private Only private Doctor visits

(1) (2) (3) (4) (5) (6) (7) (8) (9) (10)

DDD 0.021 0.226* 0.144* 0.260+ −0.084 0.056 −0.243* −0.205* 0.181** 0.266+
(0.068) (0.082) (0.052) (0.126) (0.081) (0.108) (0.081) (0.071) (0.053) (0.159)

Agg. effecta 5409 57732 36866 66329 −19614 12893 −62070 −52429 411298 632898
Avg. effectb 2.28 3.50
N 147669 147669 118375 118375 188071 188071 118375 118375 371181 371181
DD 0.073 0.296** 0.193** 0.339* −0.164* −0.006 −0.238** −0.210* 0.255** 0.353*

(0.069) (0.092) (0.056) (0.131) (0.076) (0.123) (0.069) (0.088) (0.069) (0.163)
Agg. effecta 18582 75690 49223 86510 −38148 −1487 −60815 −53623 645823 939183
Avg. effectb 3.23 4.70
N 890 890 695 695 1084 1084 695 695 2055 2055
Age trends No Yes No Yes No Yes No Yes No Yes

Means
65+, Without kidney disease
Pre 0.96 0.93 0.55 0.04 5.05
Post 0.98 0.93 0.66 0.04 4.89
65+, With kidney disease
Pre 0.92 0.91 0.43 0.04 10.35
Post 0.97 0.93 0.47 0.02 9.43
<64, Without kidney disease
Pre 0.82 0.00 0.82 0.82 3.87
Post 0.89 0.04 0.84 0.81 3.89
<64, With kidney disease
Pre 0.72 0.00 0.76 0.76 9.95
Post 0.85 0.22 0.64 0.50 11.28

a Aggregate effect of the Medicare expansion on insurance coverage and annual number of physician visits for people between 45 and 64 years of age with kidney disease
in the post period.

b Average individual effect of the Medicare expansion on the number of physician visits for people between 45 and 64 years of age with kidney disease in the post period.
Source—Author’s analysis of the National Health Interview Survey from 1968 to 1980. Notes—Dependent variable is indicated by the column group title. Kidney disease is
defined using the “Broad” definition of kidney disease (see Appendix Table A). DDD is the triple-difference coefficient from the interaction of a dummy for being under 65
years of age, a dummy for the second half of 1973 or later, and a dummy for having kidney disease; DD is the difference-in-difference coefficient from a sample with kidney
disease. Models include year, age, gender, and race fixed effects along with all one-, two-, and, if appropriate, three-way interactions of under 65, post, and kidney disease;
models with age trends also include additional interactions with age-65. Sample restricted to individuals between 45 and 84 years of age; columns (9) and (10) also exclude
people 65 years of age and data from July 1 1973 to June 30 1974. Estimates are from OLS regressions in columns (1)–(8) and Poisson in columns (9) and (10). Standard errors
clustered on age in round brackets. + p < 0.1, * p < 0.05, ** p < 0.01.

Fig. 2. Event study estimates of changes in health care utilization. Source—National Health Interview Survey, 1969–1980. Notes—Sample in panel A restricted to people
between 45 and 84 years of age; panel B uses everyone between 18 and 84 years of age, but excludes observations from the second half of 1973 and the first half of 1974.
Points in panel A are year-by-under 65 years of age-by-kidney disease coefficients from a regression of doctor visits on year fixed effects (omitted 1970), an under 65 indicator,
an indicator for kidney disease, and all two- and three-way interactions. Panel B presents point estimates for years of age interacted with a post dummy (after 1973) and
kidney disease from regressions of doctor visits on age fixed effects, post, kidney disease, and all two- and three-way interactions; smoothed line is local polynomial estimate
w lines

P t is clu
d

a
n
v
e
a

here estimates are weighted by the inverse of their standard errors and dashed

oisson regressions. Confidence intervals in panel A based on covariance matrix tha
isease defined using the “broad” definition (see appendix Table A).

fter, versus before, the Medicare expansion for people with kid-
ey disease. Panel B demonstrates that any increase in physician

isits affected virtually all ages below 65 years of age and there was
ssentially no effect on physician visits for people over 65 years of
ge.

are 95% confidence intervals of the local polynomial estimate. Estimates are from
stered on age, while panel B uses heteroskedasticity robust standard errors. Kidney

Consistent with the event studies, column 9 of Table 2 demon-
strates that the ESRD expansion was associated with a 18–25

percent increase in physician visits in models that do not con-
trol for age trends. Models that do control for age trends (column
10) yield larger estimates, which is consistent with the age profile

82 M.S. Andersen / Journal of Health Economics 60 (2018) 75–89

Fig. 3. Event study estimates of the ESRD program and mortality. Source—Author’s analysis of multiple cause of death files, 1968–1978. Notes—Sample in panel A restricted
to deaths to people between 45 and 84 years of age; panel B uses everyone between 25 and 84 years of age. Points in panel A are year-by-under 65 years of age-by-kidney
disease coefficients from a regression of the cause-age-gender-time period mortality rate on on year fixed effects (omitted 1972), an under 65 indicator, an indicator for
kidney disease, and all two- and three-way interactions. Panel B presents point estimates for years of age interacted with a post dummy (after 1973) and kidney disease from
regressions of the cause-age-gender-time period mortality rate on age fixed effects, post, kidney disease, and all two- and three-way interactions; smoothed line is local
p d erro
E ovari
s . Caus

o
g
4
n
d

d
m
a

(

4

4

t
o
r
t
n
w
e
a

i
p
p
i
i
e
w
t
w
a

a

d

olynomial estimate where estimates are weighted by the inverse of their standar
stimates are from Poisson regressions. Confidence intervals in panel A based on c
tandard errors. Kidney disease defined using the “narrow” definition (see Table A)

f the change in physician visits from panel B of Fig. 1. In aggre-
ate, my DDD estimates indicate that there were an additional
00000–600000 physician visits per year among people with kid-
ey disease, or an additional 2.3–3.5 visits per person with kidney
isease (“Avg. Effect” row).5

As was the case with my insurance estimates, my difference-in-
ifference results are generally comparable, although larger, than
y triple-difference estimates and this extends to the aggregate

nd average effects of the expansion on doctor visits.
These results are essentially unchanged in donut regressions

online appendix Table B1, columns 9 and 10).

.3. Mortality effects

.3.1. Comparisons within the United States
Fig. 3 plots event studies for kidney disease mortality using

he underlying cause of death, where the event studies are based
n triple-difference estimates. Panel A indicates that there was a
eduction in mortality due to kidney disease in 1973 and visually,
his reduction was larger than the potential downward trend in kid-
ey disease mortality prior to 1973. Panel B demonstrates that there
as a strong age trend in the mortality change following the ESRD

xpansion, which justifies focusing on specifications that include
ge trends.

In triple difference models based on equation (3) and difference-
n-differences estimates based on equation (4) I find that the ESRD
rogram reduced mortality from kidney disease by 36.3–37.3 log
oints in a model that does not include age trends. This estimate

s, at first blush, implausibly large and reflects the age trends seen
n panel B of Fig. 3. Including age trends (column 2) yields smaller
stimates of a 7.3–7.9 log point reduction in mortality. In models
ith age trends, I also find that the DD estimate is larger in magni-

ude (although not significantly so) than the DDD estimate, which is
hat one would expect from the lower level of Medicare eligibility

mong people without kidney disease.
Because there are many potential diagnoses that may indicate

death due to kidney disease, in columns (5) and (6) I present

5 There were approximately 180,000 people who met my definition of kidney
isease per year between 45 and 64 years of age.

rs and dashed lines are 95% confidence intervals of the local polynomial estimate.
ance matrix that is clustered on age, while panel B uses heteroskedasticity robust
e-age-gender-time period cells weighted by population.

results using the “broad” definition of kidney disease. The broad
results are qualitatively similar and also indicate a reduction in
mortality based on kidney disease as the underlying cause of death,
but not when kidney disease is defined using both underlying and
contributing cause of death codes.

Lastly, the ESRD program, in particular, was targeted at people
with chronic kidney disease, so in columns (7) and (8) I restrict my
definition of kidney disease to people who died of chronic kidney
disease, based on the codings in appendix Table A. The chronic esti-
mates indicate that the Medicare expansion was associated with a
reduction in deaths due to chronic kidney disease, although three
of the estimates are only significant at the ten percent level.

Table 3 also presents the change in the mortality rate and the
implied number of deaths averted, based on population data from
1973 and the average mortality rate due to kidney disease before
the Medicare expansion. Under the narrow definition and without
age trends, the Medicare expansion appears to have reduced the
mortality rate by 2.0–2.3 deaths per 100,000 for a total of between
800 and 900 fewer deaths per year due kidney disease. However,
these estimates are significantly narrowed in models that include
age trends (columns 2 and 4) to a reduction of 0.5–0.8 deaths per
100,000 or 170–320 fewer deaths. The fact that there is a greater
reduction in the number of deaths using both underlying and con-
tributing causes of death, versus just underlying causes of death,
indicates that at least part of the reduction in mortality that I
observed in column (2) is not due to a change in coding practices in
which kidney disease was less likely to be listed as an underlying
cause of death, but more likely to be listed as a contributing cause
of death.

Repeating the change in mortality analysis for both the broad
and chronic definitions yields two interesting results. First, the vast
majority of the reduction in kidney disease deaths is arising from
fewer deaths due to chronic disease, particularly when using both
underlying and contributing causes. Second, while there is a larger
reduction in mortality under the broad definition when I only look
at underlying cause of death codes, I actually find that there were
fewer deaths averted under the broad definition than the narrow

definition when I use both underlying and contributing causes of
death.

M.S. Andersen / Journal of Health Economics 60 (2018) 75–89 83

Table 3
Poisson estimates of the effect of the ESRD program on mortality.

Narrow definition Broad definition Chronic only

(1) (2) (3) (4) (5) (6) (7) (8)

A: Ages 45–84
DDD −0.373** −0.073* −0.059** −0.021* −0.067** −0.010 −0.057* −0.020+

(0.049) (0.029) (0.007) (0.010) (0.011) (0.009) (0.027) (0.012)
� in mortality rate −2.0 −0.5 −2.3 −0.8 −0.8 −0.5 −0.3 −0.7
� in # deaths −772 −174 −891 −323 −311 −196 −114 −270
DD −0.363** −0.079* −0.048** −0.025+ −0.073** −0.015 −0.064+ −0.024+

(0.053) (0.035) (0.014) (0.014) (0.022) (0.011) (0.034) (0.014)
� in mortality rate −2.0 −0.5 −1.9 −1.0 −0.9 −0.7 −0.3 −0.9
� in # deaths −755 −189 −723 −388 −337 −288 −128 −331
B: Ages 45–60 and 70–84
DDD −0.446** −0.148** −0.080** −0.066** −0.144** −0.040** −0.134* −0.062**

(0.052) (0.049) (0.006) (0.017) (0.021) (0.011) (0.053) (0.021)
DD −0.437** −0.150* −0.068** −0.065* −0.145** −0.040+ −0.136* −0.062*

(0.056) (0.066) (0.015) (0.026) (0.043) (0.021) (0.069) (0.026)
Age trends No Yes No Yes Yes Yes Yes Yes
Underlying only? Yes Yes No No Yes No Yes No
Mean annual kidney disease mortality rates (per 100,000)
Ages 45–64
1968–1973H1 6.6 6.6 40.0 40.0 13.8 52.0 5.6 36.5
1973H2–1978 5.4 5.4 37.3 37.3 8.9 45.3 4.6 32.6
Ages 65–84
1968–1973H1 28.0 28.0 251.0 251.0 100.4 368.1 24.4 238.2
1973H2–1978 32.4 32.4 241.1 241.1 76.7 323.2 27.4 218.6

Source—Author’s analysis of Multiple Cause Mortality Files for 1968–1978.
Notes—Dependent variable is the mortality rate in the age-time-gender-cause of death cells, where time is measured in half-year increments. Definitions of kidney disease
based on codes in Table A. DDD is the triple difference coefficient for being under 65, in the post expansion period, with kidney disease; DD is the difference-in-differences
coefficient for being under 65 and in the post expansion period using a sample that is restricted to deaths due to kidney disease.
Change in mortality rate is calculated as the exponentiated coefficient minus 1 multiplied by the pre-period mortality rate; change in number of deaths is the change in the
mortality rate multiplied by the population between 45 and 64 years of age in 1973. Models that do not restrict to underlying causes of deaths also define a death as due to
kidney disease if kidney disease is either an underlying or a contributing cause of death. All models include time fixed effects (measured in six month increments), age fixed
effects, an indicator for female, and all possible interactions of an indicator for being under 65, a post period dummy, and, where appropriate, an indicator for deaths due to
kidney disease. Models with age trends also include interactions with age minus 65 in addition to the under 65, post, and kidney disease interactions. Sample is restricted
t eaths

s

a
c
m
e
b
d
r
C
a
t
c
s
a
h

w
i
d
f
u
(
i
e
t
i
(

r
i

mortality (Honoré and Lleras-Muney, 2006). The bias due to com-
peting risks is similar to the bias from harvesting, but now it is the
mortality rate due to non-kidney causes that is inflated. Notably,

o deaths to whites between 45 and 84 years of age in panels A; panel B excludes d
tandard errors two-way clustered on age and time in round brackets.

The fact that there are fewer deaths averted using underlying
nd contributing cause of death codes versus just the underlying
ause of death codes under the broad definition is unexpected. One
ight expect that under a more relaxed definition of kidney dis-

ase mortality the opposite would occur. The break in the pattern
etween underlying and underlying and contributing mortality
oes not reflect a change in coding practices since there were no
elevant changes in the coding manuals published by the National
enter for Health Statistics during this time period. However, what
ppears to be happening is that there is essentially no change in
he number of deaths that list one of the more tenuously related
ause of death codes as a contributing cause of death. Given the
et of broad cause of death codes, it is not surprising that there is

smaller change in the number of deaths that list, for example,
ypertension as a contributing cause of death.

The mortality reductions in panel A of Table 3 can be combined
ith the estimated change in insurance coverage from Table 2 to

nfer how large an effect insurance coverage may have on kidney
isease mortality. Using either the increase in insurance coverage
rom column (2) or the increase in Medicare coverage from col-
mn (4) implies that there was a reduction of 0.4 percentage points
any insurance) or 0.33–0.35 percentage points (using the increase
n Medicare coverage) in the probability of dying from kidney dis-
ase associated with insurance coverage. These estimates are about
hree times larger than the local average treatment effect of Med-
caid coverage estimated by the Oregon Health Insurance Study
column (3) of Table IX in Finkelstein et al., 2012).

Alternatively, one can compute the elasticity of mortality with
espect to insurance coverage. From Table 2, the percentage change
n insurance coverage is 0.31 based on the DDD estimate for any

to people between 61 and 69 years of age. Estimates are from Poisson regressions,

insurance coverage and 0.41 using the DD estimate. Using the point
estimates in Table 3 yields an elasticity of mortality using the nar-
row, underlying definition of −0.23 using the DDD and −0.19 using
the DD estimate, which is twice as large as the elasticity from the
Oregon Health insurance Study.6

There are two main threats to the validity of my results that are
unique to mortality data. First, there is a reverse “harvesting” effect,
in which people who would have died of kidney disease in the
absence of the program are able to survive until they turn 65 after
the program. The implication of this kind of harvesting is that the
mortality rate among people 65 and older will be overstated. I am
able to test for this possibility by re-running my underlying models
while excluding people between 60 and 70 years of age (panel B).
In these donut regressions, my results are essentially unchanged
and, in fact, my estimated mortality reductions become larger. This
is inconsistent with reverse harvesting, which would predict that
the mortality reductions would be smaller in magnitude when I
exclude people between 60 and 70 years of age.

The second threat is that people who do not die of kidney dis-
ease will die of something else. This “competing risk” effect is well
known in economics and epidemiology and cannot be resolved
without imposing assumptions on the processes that determine

6 To calculate the elasticity, I first calculated the fraction of the controls who died
by the end of the study (0.8 percent) to get an implied percentage change in mortality
of 16.25% ( 0.0013

0.008 ). The first-stage statistics (Table 3) implies a percentage change in
Medicaid coverage of 182%. The resulting elasticity is 0.09 ( 0.1625

1.816 ).

84 M.S. Andersen / Journal of Health Economics 60 (2018) 75–89

Fig. 4. Cross-country event study estimates of the ESRD program and mortality. Source—Author’s analysis of the World Health Organization Mortality Database for 1968
through 1978. Notes—Sample restricted to deaths to people between 45 and 84 years of age. Points in panel A are year-by-under 65 years of age-by-kidney disease-by-United
States coefficients from a regression of the cause-age-gender-year-country mortality rate on year fixed effects (omitted 1972), an under 65 indicator, an indicator for kidney
disease, and an indicator for the United States and all two-, three-, and four-way interactions. Panel B presents point estimates for years of age interacted with a post dummy
( nder-
a ions. C
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M
a
d
t

after 1973), kidney disease, and United States from regressions of the cause-age-ge
nd all two-, three-, and four-way interactions. Estimates are from Poisson regress
eighted by population.

ompeting risks can only bias my estimates if there is, in fact, an
ffect of the Medicare expansion on kidney disease mortality. In the
bsence of such a reduction, there is no reason to expect to find a
ompeting risk bias. I can address the bias from competing risks by
estricting my data to deaths due to kidney disease, in other words
he DD results are not subject to competing risks. My DD results
emonstrate that any bias from competing risks is small since my
D estimates are, in general, larger in magnitude than the DDD
stimates (which is also the relationship one would expect to hold
f the treatment effect of Medicare eligibility was of the same sign
or people with and without kidney disease).

The online appendix presents results from a log-linear OLS spec-
fication, which are qualitatively similar (Table B2). The online
ppendix also provides robustness tests of the triple and double-
ifference results by varying the range of ages included (online
ppendix Fig. A1) and varying the age and time controls that are
ncluded (Table B3).

In the online appendix (Table B4), I also consider the potential
onfounding effect of the introduction of the Supplemental Secu-
ity Income (SSI) program in 1974. The SSI program provides cash
ransfers to low-income people who are aged, blind, or disabled
nd, in most states, also provides access to Medicaid coverage. To
est if the SSI program is confounding my estimate of the effect
f the SSDI program, I interacted the triple difference coefficients
ith (demeaned) shares of people in an age-gender-state cell who

eported either Social Security or SSI income in the March CPS from
977 to 1979 (covering years 1976 to 1978). In a separate specifi-
ation, I interacted the triple difference coefficients with indicators
or two factors that states can use to discourage enrollment in

edicaid–using more stringent eligibility criteria and requiring a
eparate Medicaid application. I find no evidence that these interac-
ions are statistically significant using either the narrow or chronic
efinitions of kidney disease, indicating that the SSI program is not
riving the differential mortality reduction for kidney disease, rela-
ive to other causes of death. However, I do find that more stringent

edicare criteria and separate Medicare applications are associ-
ted with increase mortality under the broad definition of kidney
isease, indicating that there was an increase in mortality from

hese other cause of death codes.

year-country mortality rate on age fixed effects, post, kidney disease, United States,
onfidence intervals are clustered by country, cause-age-gender-year-country cells

4.3.2. Comparisons with other OECD countries
Fig. 4 plots event-study estimates of the change in kidney dis-

ease mortality in the United States, relative to other OECD countries
by either year (panel A) or age (panel B). Over time, there is a pro-
nounced reduction in kidney disease mortality for people under 65
in the United States in 1973 that was not observed in other coun-
tries. However, there is also some evidence of a trend in kidney
disease mortality in the United States towards fewer people under
65 dying from kidney disease, although with one exception, all of
the confidence intervals before 1972 include 0. Despite the possible
violation of the parallel trends assumption, there is still evidence
of a substantial reduction in kidney disease mortality beginning in
1973. Results by age (panel B) are also suggestive of a reduction in
kidney disease mortality, although there appears to be a reduction
in mortality among 65–70 year olds, relative to people 70 and older,
in the data as well.

Going from the event-study estimates in Fig. 4 to triple and
quadruple difference results, I find that the ESRD program was
associated with a four to eight log point reduction in mortality
from kidney disease, depending upon the specification and sample
(Table 4). This reduction in mortality is robust to including country
fixed effects, interacting country fixed effects with either kidney
disease or an indicator for 1974 or later (the post dummy takes the
value 0.5 in 1973), and including year-by-kidney disease indicators,
which accounts for innovations in the treatment of kidney disease.
These results are also similar in magnitude to my results using
the narrow definition of kidney disease and underlying cause of
death codes in the US mortality data, which is the most comparable
specification.

5. Mechanisms

The ESRD expansion may have affected health through two
classes of mechanisms. First, by lowering the cost of accessing
treatment, health insurance may have increased demand for renal
replacement services (dialysis and kidney transplantation), which
would have been otherwise unaffordable. This mechanism implies

that there may be an “access motive” to purchase health insurance
in the sense of Nyman (1999, 2003, 1999) and, in essence, reflects
the fact that the Medicare expansion provided a large in-kind trans-
fer from healthy people to those with ESRD.

M.S. Andersen / Journal of Health Economics 60 (2018) 75–89 85

Table 4
Cross-country estimates of the effect of the ESRD program on kidney mortality.

(1) (2) (3) (4) (5) (6) (7) (8)

DDDD −0.064** −0.077** −0.064** −0.076** −0.057** −0.064** −0.058** −0.065**
(0.023) (0.024) (0.024) (0.024) (0.020) (0.023) (0.020) (0.023)

DDD −0.048* −0.060** −0.045* −0.048* −0.039* −0.040*
(0.023) (0.022) (0.020) (0.021) (0.017) (0.018)

Only members before 1969 No Yes No Yes No Yes No Yes
Country FE X X X X X X
Country interactions X X X X
Year-by-kidney X X

Source—Authors’ analysis of the World Health Organization Mortality Database for 1968 through 1978, covering the United States and OECD Member States at any point in
time.
Notes—Coefficients are point estimates from Poisson regressions using the mortality rate per 100,000 in each country-year-gender-age group-cause of death cell as the
dependent variable. DDDD is the coefficent on the four-way interaction of a dummy for the United States, an indicator for the post period, a dummy for deaths due to kidney
disease, and a dummy for being 45–64 years of age; DDD is the corresponding coefficient in models that restrict to deaths due to nephritis. All models include year, age, and
gender fixed effects and trends in age-65, where age in each cell was recentered by 2.5 years. Country Interactions are two-way interactions of country fixed effects with
dummies for kidney disease and post. Sample restricted to individuals between the ages of 45 and 84 and years in which the country used the ICD-8 coding regime.
Estimates are from Poisson regressions, cells weighted by population, standard errors clustered on country in parentheses.
+ p < 0.1, * p < 0.05, ** p < 0.01, *** p < 0.001.

Table 5
In-state treatment capacity and mortality reduction.

Narrow definition Chronic only

(1) (2) (3) (4) (5) (6)

A: Base model
DDD −0.077** −0.076* −0.078* −0.060* −0.058+ −0.061+

(0.028) (0.031) (0.033) (0.028) (0.031) (0.032)
×Log dialysis clinics
Per Capita in 1971 −0.065** −0.093** −0.062* −0.086*

(0.023) (0.033) (0.025) (0.037)
×Log transplant programs
Per Capita in 1971 −0.008 0.061 −0.009 0.057

(0.060) (0.063) (0.058) (0.065)
B: Including indicators for VA treatment facilities
DDD −0.080** −0.077* −0.081* −0.063* −0.059* −0.064*

(0.029) (0.031) (0.032) (0.029) (0.029) (0.031)
×Log dialysis clinics
Per Capita in 1971 −0.067** −0.082* −0.065* −0.076*

(0.025) (0.037) (0.027) (0.037)
×Log transplant programs
Per Capita in 1971 −0.016 0.044 −0.017 0.037

(0.058) (0.065) (0.057) (0.064)

Source—Author’s analysis of Multiple Cause Mortality Files for 1968–1978 and the publication “Kidney Disease Services, Facilities, and Programs in the United States” (Kidney
Disease Program, 1971).
Notes—Dependent variable is the mortality rate in the state-age-time-gender-cause of death cells, where time is measured in half-year increments. Definitions of kidney
disease based on codes in Table A. DDD is the triple difference coefficient for being under 65, in the post expansion period, with kidney disease; models with interactions of
DDD with either dialysis clinics or transplant programs also include all two- and three- way interactions of dialysis clinics or transplant programs with under 65, post, and
the kidney disease indicator. Models also include indicators for having no dialysis clinics or transplant programs in a state; panel B also includes indicators for the presence
of VA dialysis clinics and transplant programs (also interacted with DDD). All measures of dialysis clinics and transplant programs have been demeaned. All models include
state, time, and age fixed effects, an indicator for female, and age trends interacted with under 65, post, and kidney disease.
Sample is restricted to deaths to whites between 45 and 84 years of age. Estimates are from Poisson regressions, standard errors three-way clustered on state, age, and time
i
+

p
s
f
r
d
t
h
a

5

t
a

n round brackets; each state weighted by its total population.
p < 0.1, * p < 0.05, ** p < 0.01.

The second class of mechanisms relate to changes in the sup-
ly of renal replacement services. The expansion did not merely
hift the demand curve outward, but it also guaranteed payment
or treatment services, which reduced the risk of investing in renal
eplacement services. In much the same way that the original intro-
uction of Medicare stimulated entry by hospitals and increased
echnology adoption (Finkelstein, 2007), the ESRD expansion may
ave increased adoption and entry of renal replacement services
cross the country.

.1. Access to care

In order to test if access to care was an important contributor
o the reduction in mortality associated with the ESRD expansion, I
ugmented Eq. (3) with interactions between the triple-difference

variables and measures of the number of dialysis clinics and trans-
plant programs per capita. Table 5 presents the results of this
analysis. Panel A demonstrates that living in a state with more dialy-
sis clinics in 1971 was associated with a significantly larger decline
in kidney disease mortality, but there was no effect of living in a
state with a transplant program. These results persist, even after
I include indicators for the presence of Veteran’s Administration
dialysis clinics and transplant programs (panel B).

The lack of evidence that transplant programs affect local mor-
tality is not surprising since transplant programs require fewer
visits than dialysis clinics. Therefore patients may be willing to

travel long distances in order to get a kidney transplant, mean-
ing that the number of programs in a state is not the most relevant
metric affecting their survival.

86 M.S. Andersen / Journal of Health Economics 60 (2018) 75–89

Table 6
Entry of dialysis and transplant facilities.

Per 100,000 in 1975

Dialysis clinics Transplant programs

(1) (2) (3) (4) (5) (6)

Log per capita
Dialysis clinics 0.316* 0.356** 0.379**

(0.127) (0.090) (0.091)
Transplant programs 0.710** 0.577** 0.551**

(0.154) (0.108) (0.123)
Log kidney disease mortality rate

Under 65 0.367+ 0.288 0.660* 0.780*

(0.197) (0.222) (0.275) (0.364)
65 and Over 0.320 −0.282

(0.284) (0.595)
Constant −0.381 −0.693* −1.421 −0.500 −1.615** −0.805

(0.260) (0.292) (1.054) (0.437) (0.581) (1.770)

Source—Author’s analysis of Multiple Cause Mortality Files for 1971, the publication “Kidney Disease Services, Facilities, and Programs in the United States” (Kidney Disease
Program, 1971) and the 1977 Social Security Bulletin. See text for details.
Notes—Independent variables are measured in 1971, kidney disease mortality rate averaged from 1968 to 1971. Kidney disease mortality defined using the “narrow” definition
a iven t
+

i
l
f
t
t
p
d

5

i
b
a
m
p
t
t

W
t
e
s
i
1
n
s
m
c
m
t
i

r
t
B

nd underlying causes of death. Models also include indicators for no facilities of a g
p < 0.1, *p < 0.05, **p < 0.01.

The implication of these results is that either the ESRD program
ncreased the number of dialysis clinics in states that already had a
arge number of clinics, relative to population, or that the program
acilitated access to the existing clinic network. In the next subsec-
ion, I test if the number number of dialysis clinics per capita after
he expansion increased more in areas with more dialysis clinics
er capita in 1971, or if there was greater entry in areas with fewer
ialysis clinics per capita.

.2. Entry of treatment facilities

The ideal data with which to test the entry hypothesis would
nvolve regressing the change in treatment facilities on the num-
er of people for whom dialysis or kidney transplantation was
ppropriate. However, such data are not available. Instead, I use the
ortality rate due to kidney disease as a proxy. The idea behind this

roxy is that in areas with a higher mortality rate there are likely
o be more people for whom treatment is appropriate. Therefore,
o test the entry hypothesis, I estimate the following model:

ln E

[
y1975

s

pop1975
s

]
= ˛0 + ˛1 ln

(
y1971

s

pop1971
s

)
+ ˛2 ln MortPre

s,<65

+˛3 ln MortPre
s,≥65 + ˛41

[
y1971

s = 0
] (5)

here the model is estimated as a Poisson regression, s denotes
he state, superscripts refer to the year to which the data refer, yt

s is
ither the number of dialysis clinics or transplant programs in state

at time t, popt
s is the population in state s and year t, and MortPre

s,g
s the average annual kidney disease mortality rate from 1968 to
971 using the “narrow” definition with deaths to attributed kid-
ey disease based on the underlying cause of death codes in state

for age group g (either under 65 or 65 and older).7 ˛1 tests if the
easure of treatment programs in a state is converging across the

ountry depending on whether or not the elasticity of 1975 treat-

ent capacity with respect to 1971 treatment capacity is greater

han, less than, or equal to one. ˛2 and ˛3 test if treatment capacity
s responsive to the burden of disease in the area since areas with

7 Using the 1971 kidney disease mortality rate yield similar, but less precise,
esults for dialysis clinics and significantly smaller estimates of the elasticity of
ransplant programs with respect to the mortality rate, see online appendix Table
5.

ype in 1971. Estimates from Poisson models, robust standard errors in parentheses.

a greater burden of disease will have a higher mortality rate due to
kidney disease. A priori one would expect ˛2 > 0 and ˛3� 0 as indi-
cators that the Medicare expansion, since it affected people under
65 years of age, encouraged entry.

Table 6 demonstrates that the number of dialysis clinics
(columns 1–3) was converging over time since the coefficient on
1971 treatment capacity is less than one. In other words, states
with comparatively few dialysis clinics, relative to population, in
1971 experienced a more rapid rate of increase than did states
with more dialysis clinics per capita in 1971. Furthermore, there
is some evidence that mortality among people under 65 served to
increase the number of clinics in a state in 1975, which is consis-
tent with the Medicare expansion encouraging entry of new dialysis
clinics, although the mortality effect disappears when I also include
mortality among people 65 and over.

Column 4–6 demonstrate that the pattern of convergence was
weaker for transplant programs, but that there was a substantially
larger effect of under 65 mortality on the entry of transplant pro-
grams than for dialysis clinics.

The fact that there was more rapid convergence for dialysis clin-
ics than transplant programs is consistent with differences in how
these two forms of treatment are used. Dialysis clinics require that
patients return frequently for treatment since the typical treatment
regimen may include as many as five treatments per week, as a
result proximity to a dialysis clinic is important, hence one would
expect to see a large increase in dialysis clinics. On the other hand,
kidney transplant programs require fewer visits so that patients
may be willing to travel long distances in order to get a kidney trans-
plant, meaning that there is less need for a uniform distribution of
transplant programs across the country.

6. Welfare implications

These results provide some insight into the welfare conse-
quences of the Medicare expansion among people with kidney
disease, specifically the productivity of moral-hazard induced care.
One typically thinks of moral-hazard induced care as inefficient
since it is care that the consumer was unwilling to pay for at the
offered price (Pauly, 1968). However, one can recast this framework

in terms of the marginal health product of health care and a con-
sumer’s willingness to pay for a unit of health. In this framework, a
consumer’s willingness to pay for health care is decreasing because
either the marginal health product is decreasing or her valuation

M.S. Andersen / Journal of Health Economics 60 (2018) 75–89 87

Table 7
Impact of the ESRD program on life expectancy at age 45.

Narrow definition Broad definition Chronic only

(1) (2) (3) (4) (5) (6) (7) (8)

Actual
Survival to age 64 18.36 18.36 18.36 18.36 18.36 18.36 18.36 18.36
Survival to age 84 28.83 28.83 28.83 28.83 28.83 28.83 28.83 28.83

DDD counterfactual
Survival to age 64 18.36 18.36 18.36 18.36 18.36 18.36 18.36 18.36
Difference from actual 0.003 0.001 0.003 0.003 0.002 0.002 0.001 0.002
Life years saved 7235 2189 7641 7883 4618 5045 1291 5117

Survival to age 84
28.84 28.83 28.84 28.84 28.84 28.84 28.83 28.84

Difference from actual 0.007 0.002 0.008 0.007 0.005 0.005 0.001 0.005
Life years saved 17671 5085 19546 17451 11025 11201 3043 11655

DD Counterfactual
Survival to age 64 18.36 18.36 18.36 18.36 18.36 18.36 18.36 18.36
Difference from actual 0.003 0.001 0.003 0.005 0.003 0.005 0.001 0.004
Life years saved 7074 2974 6200 12429 6080 11234 1999 9415

Survival to age 84
28.84 28.83 28.84 28.84 28.84 28.84 28.83 28.84

Difference from actual 0.007 0.003 0.007 0.011 0.006 0.010 0.002 0.009
Life years saved 17278 6699 15857 26992 14152 24274 4500 20687

Age trends No Yes No Yes Yes Yes Yes Yes
Underlying only? Yes Yes No No Yes No Yes No

Source—Author’s analysis of Multiple Cause Mortality Files for 1968–1978.
Notes—Based on estimates from models presented in Table 3. “DDD Counterfactual” uses DDD estimates from Table 3 and “DD Counterfactual” uses DD estimates. Coun-
t releva
c on p

o
o
c
(
t

l
p
t
m
t
p
e
o

i
t
g
t
n
c
t
t
t
i
t
w
o
f

s
c

b

erfactual survival is based on multiplying kidney-specific mortality hazard by the

umulative survival probabilities by age (see text for details). Life years saved based

f a unit of health is decreasing. Assuming that a person’s value
f a unit of health is fixed (or at least unlikely to change signifi-
antly) then the downward slope of demand curves for health care
and the resulting welfare losses from moral hazard) come from
he decreasing marginal product of health care.

In this paper, I provide suggestive evidence of an increase in uti-
ization of dialysis facilities. First, I find an increase in self-reported
hysician visits in the NHIS, which includes dialysis care. Second,
he reduction in kidney disease mortality was larger in areas with

ore dialysis clinics in 1971. Collectively, these results suggest that
he increase in dialysis clinic visits had a positive marginal health
roduct. Whether or not this health impact was large enough to
liminate the welfare cost of the increase in consumption depends
n the size of the health improvement.

I can quantify the size of the health improvement by comput-
ng the change in survival associated with the program and, from
here, calculating the number of life years saved due to the pro-
ram. In order to estimate the survival gains, I begin by computing
he age- and gender-specific average mortality hazard due to kid-
ey and non-kidney causes in the pre period. In order to compute
ounterfactual survival, I then multiply the mortality hazards due
o kidney disease for people under 65 years of age by the exponen-
iated triple difference or difference-in-difference coefficient from
he models in Table 3. In order to combine these mortality hazards
nto a single hazard that I can use to calculate survival, I assume
hat latent survival durations from kidney and non-kidney causes

ere independent so that the mortality hazard at age a is the sum

f the cause specific mortality hazards at age a.8 I compute survival
rom age 45 as the sum of the cumulative survival probabilities9 and

8 Assuming that survival durations are independent is a strong assumption, but
ome assumption is needed in order to evaluate treatment effects in this kind of a
ompeting risks framework (Honoré and Lleras-Muney, 2006).

9 Suppressing all subscripts other than age, if the mortality rate at age a is denoted

y ma then the survival duration is S =
∑84

a=45

[
exp

(∑a

a′=45
log (1 − ma′ )

)]
.

nt coefficient for cells under age 65 and then computing survival as the sum of the
opulation of white and non-white 45 year olds.

compute the differences from the survival durations implied by the
pre-period mortality rates. I then convert these differences, which
are representative of the effects on a 45 year old, into population-
level estimates by multiplying by the population of white 45 years
olds in 1973, which yields an estimate of the number of life years
saved by the Medicare expansion’s effect on kidney disease mor-
tality and, therefore, the productivity of the induced health care
utilization.

Table 7 presents the results of this analysis. In column (2), which
reports results using the narrow definition and with age trends, in
the first panel I report that life expectancy from age 45 is 18.36 years
up to age 65 and almost 29 years to age 85 (I am unable to calcu-
late subsequent mortality hazards since I do not have denominator
data for people 85 and older). Using the triple-difference coeffi-
cients there is almost no change in survival—life expectancy rose
by 0.001 years to age 64 and by 0.002 years to age 84. However,
these estimates are for the entire population while only a small
minority actually has kidney disease. When I scale these estimates
by the number of white and non-white 45 year olds, I find that the
expansion saved between 2200 and 5100 life years, depending on
the age cutoff used. I find larger savings using the difference-in-
difference estimate to construct the counterfactual mortality rates.
Applying a value of $100,000 to a life year, the results in column (2)
imply that the mortality benefits of the Medicare expansion due
to changes in kidney disease mortality were worth between $220
million and $670 million per year. Spending on this population in a
single year was around $750 million indicating that the program

cannot be justified solely based on its effects on kidney-related
mortality.10 However, using some of my more relaxed specifica-
tions (e.g. including contributing causes of death) implies that the

10 I assumed that there were 11500 beneficiaries between 45 and 65 years of age
based on the age distribution of people who were eligible for Medicare only because
of ESRD (people who did not also have a long-term disability) and that spending per
person was $64,500 per year in 2015 dollars.

8 ealth E

v
i
a
c
a

a
d
2
a
a

s
t
H
i
o
d
f
a
b

7

e
e
p
i
s

i
m
C
d
y
i
c
s

n
t
c
a
h
1

l
2
C
B
1
s
H
l
b
p
s
t
m
t
w

)

8 M.S. Andersen / Journal of H

alue of the life years saved may exceed $1 billion, indicating that
t is possible that this expansion yielded benefits in excess of costs,
ssuming that each life year was worth $100,000 and that other
osts associated with the program (e.g. spending on other services)
re not too large.

Across most of the remaining specifications, I find evidence of
n increase in survival, with estimates using underlying causes of
eath and age trends indicating that the expansion saved between
500 and 14000 life years; using contributing cause of death codes
s well yields a somewhat broader range, though the increase is not
s dramatic as with the narrow definition of kidney disease.

My welfare analysis does not consider the effect of these expan-
ions on the incidence of ESRD. In essence, I am assuming that
here is no “ex-ante” moral hazard (Ehrlich and Becker, 1972).
owever, this perspective is also consistent with my analysis not

ncluding the value that these expansions provide against the risk
f developing ESRD. Notably these two omissions act in opposite
irections–ex-ante moral hazard would tend to decrease the wel-
are benefit of the program, while the insurance value of protection
gainst a previously uncovered risk would increase the welfare
enefit of the program.

. Conclusions

In this paper, I estimated the causal effect of the 1973 Medicare
xpansions affected people with kidney disease. In aggregate the
xpansion increased insurance coverage and physician visits for
eople with kidney disease. I also document a significant reduction

n mortality due to kidney disease that was robust to a variety of
pecification checks and alternative definitions of kidney disease.

I identify two mechanisms for my results. The first mechanism
s that the increase in insurance coverage provided access to treat-

ent that was otherwise unavailable (Nyman, 1999, 1999, 2003).
onsistent with this mechanism, I find larger reductions in kidney
isease mortality for people under 65 in areas that had more dial-
sis facilities in 1971. An important implication of this mechanism
s that there is a large liquidity effect in the demand for medical
are, in which case the welfare loss from moral hazard may be
ignificantly reduced.

I also find evidence in support of a second, supply-side, mecha-
ism by which the Medicare expansion lead to increased entry of
ransplant programs and, to a lesser degree, dialysis clinics. Specifi-
ally, I find that having a higher mortality rate due to kidney disease
mong people under 65 betweenn 1968 and 1971 is correlated with
aving more dialysis clinics and transplant programs per capita in
975.

My results contribute to a large literature on the effects of pub-
ic insurance programs (Currie and Gruber, 1996, 1996; Finkelstein,
007; Finkelstein et al., 2012; Finkelstein and McKnight, 2008;
utler and Gruber, 1996; Gruber and Simon, 2008; Goodman-
acon, 2017)(e.g. Currie and Gruber, 1996a,b; Cutler and Gruber,
996; Finkelstein, 2007; Finkelstein and McKnight, 2008; Finkel-
tein et al., 2012; Goodman-Bacon, 2017; Gruber and Simon, 2008).
owever, a distinctive feature of my results, relative to others in the

iterature, is that the program that I study conditions coverage on
eing in poor health. As a result, the benchmark for evaluating this
rogram is somewhat different than for other insurance expansions
ince an effect on mortality that may seem large among a popula-

ion that was not selected on the basis of ill health, may be much

ore plausible in the context of a program that explicitly condi-
ioned eligibility on people having an expected survival of days or
eeks following diagnosis with ESRD.

conomics 60 (2018) 75–89

Appendix A.

See Table A .

Appendix A
ICD codes for kidney disease, by ICD revision.

ICD-7
(1968 NHIS)

ICDA-8
(1968–1978)

ICD-9
(1979–1980 NHIS

Narrow definition:
Chronic kidney

disease
592–594,792 582–584, 593.2, 792 582–589

Acute kidney
disease

590–591 580–581, 593.1 580–581, 584

“Broad” definition
Other diseases of

urinary system
600–609 590–599 590–599

Hypertension 442,446 403–404 403–404
NHIS omissions 604–609 594–599 594–599

Appendix B. Supplementary data

Supplementary data associated with this article can be found,
in the online version, at https://doi.org/10.1016/j.jhealeco.2018.06.
002.

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