THREE ESSAYS ON LABOR AND HEALTH ECONOMICS

By

Dajung Jun

A DISSERTATION

Submitted to

Michigan State University

in partial fulﬁllment of the requirements

for the degree of

Economics — Doctor of Philosophy

2019

ABSTRACT

THREE ESSAYS ON LABOR AND HEALTH ECONOMICS

By

Dajung Jun

In chapter 1, I investigate the eﬀectiveness of tax credits on health insurance premiums.

There was a renewed interest in using tax credits to increase health insurance coverage after

the push to repeal the Aﬀordable Care Act (ACA). The Health Insurance Tax Credit (HITC)

was implemented between 1991–1993 to reduce the burden of health insurance premiums

primarily for low-income families. Although it was active for three years, this policy has

been studied in only one previous study. In this chapter, I examine the eﬀectiveness of the

HITC by using the Survey of Income Program Participation (SIPP), and I provide the ﬁrst

estimates of its eﬀects on healthcare utilization and selfreported health status. My results

align with previous studies and suggest the HITC increased the health insurance take-up

by 5.8 percentage points. The implementation of the HITC also signiﬁcantly improved the

self-reported health status of respondents.

In the second chapter, I analyze the eﬀects of dependent coverage mandates on working

fathers job mobility and compensation. Due to the low rates of health insurance coverage

among young adults, some state governments began mandating health insurance companies

to allow adult children to stay on their parents’ health insurance plans. First implemented

in 1995, these mandates aimed to increase health coverage among young adults. In 2010,

the federal government enacted a more comprehensive version of the dependent coverage

mandate as part of the Aﬀordable Care Act. These state- and federal-level eﬀorts successfully

increased insurance rates for young adults, but they might have also come with unintended

consequences for parents. Parents who placed a high value on health insurance for their young

adult children might be reluctant to leave jobs with employer-provided health insurance, and

employers might oﬀset the mandated-incurred health care costs by reducing other types of

employee beneﬁts or earnings. To assess the extent of such consequences, I study the eﬀects of

both the state and federal dependent health insurance mandates on fathers. By analyzing the

2004 and 2008 SIPP panels, which are linked with Detailed Earnings Records and Business

Registrar data from the United States Census, I examine the mandates’ eﬀects on fathers’

voluntary job separation rates (job-lock and job-push) and changes in their compensation.

After the implementation of the mandates, I observe a signiﬁcant decrease in the likelihood of

voluntary job separation among eligible working fathers aged 45–64 with employer-provided

health insurance.

In the last chapter, we investigate the impact of lifetime earnings on retirement wealth.

Venti and Wise (1999, 2001) directly examine this question by utilizing data that was superior

to that available to previous researchers and conclude that “the bulk of the dispersion must

be attributed to diﬀerences in the amount that households choose to save.” In this paper,

we examine the extent that a remaining problem in their data aﬀected their results: Their

measure of lifetime earnings, despite being based on administrative data, was subject to

topcoding in each year. Using the 2001 SIPP that was not subject to the same problem,

we ﬁnd that the eﬀect of the topcoding was substantial. At least 35 percent of individuals

were misclassiﬁed in each of the top four deciles. When replicating a key result of Venti and

Wise (2001), our ﬁndings suggest that the correlation between lifetime earnings and savings

was about 50% greater than what was found when using censored deciles. This increased

explanatory power came largely at the expense of the other variables in the regression model.

Copyright by
DAJUNG JUN
2019

To my parents

and my brother, Youjung

v

ACKNOWLEDGEMENTS

I am very grateful to my advisor Steven Haider for his support, encouragement

and helpful feedback. I would also like to thank John Goddeeris and Stacy Dickert-

Conlin for their invaluable help and advice.

I am thankful to my brother for his

encouragement over the last ﬁve years. Lastly, this could not be possible without the

loving support from my parents, who have been by my side throughout the whole

experience.

vi

TABLE OF CONTENTS

LIST OF TABLES . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

x

1 Chapter 1. Eﬀectiveness of Tax Credits for Health Insurance Pre-
mium: Evidence from the Health Insurance Tax Credit
. . . . . . .
1.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1.2 Methods
1.2.1 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . .
1.2.2 Data
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1.3 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1.3.1 Coverage Rates . . . . . . . . . . . . . . . . . . . . . . . . . . . .
1.3.2 Health-Care Utilization and Health Status . . . . . . . . . . . . .
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

1.4 Conclusions

1
1
2
2
5
6
6
11
13

APPENDIX . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 15

2 Chapter 2. The Eﬀects of the Dependent Health Insurance Cover-

age Mandates on Fathers’ Job Mobility and Compensation . . . . . 20
20
2.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
22
2.2 Institutional Details . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2.3 Literature Review . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
24
27
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2.4 Methods
27
2.4.1 Data
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2.4.2 Identiﬁcation Strategy . . . . . . . . . . . . . . . . . . . . . . . .
33
37
2.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
37
2.5.1 Job-Lock . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
2.5.2 Job-Push . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
43
44
2.5.3 Reduction in Compensation . . . . . . . . . . . . . . . . . . . . .
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
45

2.6 Conclusions

APPENDIX . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 49

3 Chapter 3. Reconsidering Venti and Wise: Choice or Chance? . . . 52
52

3.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

vii

3.2 Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
3.3 Venti and Wise’s Analysis . . . . . . . . . . . . . . . . . . . . . . . . . .
3.4 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
3.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
3.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

54
55
57
58
64

APPENDIX . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 65

BIBLIOGRAPHY . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 70

viii

LIST OF TABLES

Table 1.1 Summary Statistics, 1989-1995 . . . . . . . . . . . . . . . .

Table 1.2 Estimates from Equation (1), 1989-1993 . . . . . . . . . .

Table 1.3 Robustness Check, 1989-1993 . . . . . . . . . . . . . . . . .

7

8

8

Table 1.4 Estimates from the Equation (2), 1989-1995 . . . . . . .

10

Table 1.5 Health-Care Utilization & Self-Reported Health Status

12

Table A.1 Event History Analyses, 1989-1993 . . . . . . . . . . . . .

16

Table A.2 Change in Uninsured Coverage Rates, 1989-1993 . . . .

17

Table A.3 Private Coverage among Medicaid Enrollees, 1990-1992

Table A.4 Coverage Rates, Oﬃce Visit and Health-Status Report

18

19

Table 2.1 Examples of Childrens’ Age Eligibility by State . . . . .

30

Table 2.2 Descriptive Statistics of Fathers . . . . . . . . . . . . . . .

32

Table 2.3 Job-Lock . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

38

Table 2.4 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . .

40

Table 2.5 Heterogeneity Tests . . . . . . . . . . . . . . . . . . . . . . .

40

Table 2.6 Falsiﬁcation Tests . . . . . . . . . . . . . . . . . . . . . . . .

43

Table 2.7 Job-Push . . . . . . . . . . . . . . . . . . . . . . . . . . . . .

44

Table 2.8 Annual Earnings and Total Monetary Compensation 1 .

44

Table B.1 Implementation of the Dependent Coverage Laws . . . .

50

Table B.2 Alternative Regression Results (Logit) . . . . . . . . . . .

51

Table B.3 Annual Earnings and Total Monetary Compensation 2 .

51

Table B.4 Working Mothers’ Job Mobility . . . . . . . . . . . . . . .

51

ix

Table 3.1 Basic Descriptives for SIPP Household Sample . . . . .

59

Table 3.2 Percent of Each Uncensored Classiﬁed into Each Censored 60

Table 3.3 Comparing the Venti and Wise to Our SIPP Varibles .

61

Table 3.4 Reduction in RMSE . . . . . . . . . . . . . . . . . . . . . .

62

Table C.1 Comparing Administrative Data Availability

. . . . . .

67

Table C.2 Determining Censorship in SIPP . . . . . . . . . . . . . .

68

Table C.3 Men 51-61 Topcode Values . . . . . . . . . . . . . . . . . .

68

Table C.4 2001 SIPP Wealth Variables

. . . . . . . . . . . . . . . . .

69

x

Chapter 1. Eﬀectiveness of Tax Credits for Health Insurance

Premium: Evidence from the Health Insurance Tax Credit

D. Jun (2018). Eﬀectiveness of tax credits for health insurance premium: Evidence

from the health insurance tax credit, Health Economics 2018;18. https://doi.org/

10.1002/hec.3785

1.1 Introduction

Health insurance access and aﬀordability continues to dominate the political landscape

in the United States. Since the beginning of the Trump administration, a signiﬁcant

component of the debate is to repeal and replace the Aﬀordable Care Act (ACA), a

government-led health policy enacted in 2010. For instance, the GOP tax bill that

was recently passed includes getting rid of the individual mandate under the ACA. As

a result, there are substantial fears that this change, alongside others, could increase

premiums as healthy individuals will exit the market. A common method to reduce

the burden of premiums, and thus encourage take-up, is using tax credits.

In this paper, I revisit the eﬀectiveness of tax credits that were intended to

promote coverage take-up and health-care utilization by examining the implementation

and repeal of the Health Insurance Tax Credit (HITC). The overall circumstances of

tax credits oﬀered under the HITC diﬀer from current laws and proposals but still

provide a natural experimental setting to explore the eﬀectiveness of tax credits on

health insurance coverage and other health-related outcomes.1 To date, only Cebi and

1With the HITC, some people were given tax credits for which they were not eligible before. In contrast,
the most currently proposed bills [e.g., American Health Care Act (AHCA), Better Care Reconciliation Act
(BCBA), Obamacare Repeal Reconciliation Act (ORRA) and Health Care Freedom Act (HCFA)] often suggest
reducing those tax credits.

1

Woodbury (2014, hereafter CW) has explored the eﬀectiveness of the HITC, but they

solely examined the aspect of change in health insurance.

This paper begins by replicating CW based on a diﬀerent data set, the Survey of

Income and Program Participation (SIPP). I ﬁnd a 7.1 percentage points (pp) increase

in private health insurance coverage for low-educated, working single mothers due to the

HITC combined with the Earned Income Tax Credit (EITC). This result is somewhat

larger than the 4.7 pp increase found by CW using the Current Population Survey

(CPS). I extend the analysis to the policy change in 1994-1995 (when the EITC was

expanded and the HITC was repealed) to disentangle the eﬀect of the EITC from that

of the HITC.2 This analysis suggests that the eﬀect of the HITC alone is 5.8 pp while

CW concluded 3.6 pp by using a diﬀerent DDD approach.3 Given the consistency of

my results with the previous paper, this paper assures the eﬀectiveness of the HITC on

coverage. I also estimate the eﬀect of the HITC on health-care utilization and health

status, ﬁnding a statistically signiﬁcant improvement in health status.4

1.2 Methods

1.2.1 Empirical Strategy

The HITC was a supplement to the EITC from 1991 through 1993 and was introduced

as part of the Omnibus Budget Reconciliation Act of 1990. It was a refundable tax

credit available to EITC-eligible taxpayers who purchased private health insurance and
2The increase in the maximum amount of credits through the EITC (by $239 in 1991, $132 in 1992 and
$110 in 1993) has the potential to elevate the demand for health insurance. Therefore, it is problematic to
identify the eﬀect of the HITC per se on coverage without considering the policy change in 1994-1995.

3While my analysis is based on 1989-1995, CW instead enlarges the sample by adding earlier years going

back to 1985 to isolate the eﬀect of the HITC.

4It is reasonable to hypothesize that if low-income populations experienced a signiﬁcant increase in insur-
ance enrollment, then the eﬀects of health-care utilization and health status in the active-HITC period might
have subsequently increased.

2

had at least one child covered. The HITC was structured to vary by earned income.5

To examine how the adoption of the HITC with a parallel increase in the EITC

aﬀected single mothers, I ﬁrst follow a diﬀerence-in-diﬀerences (DD) strategy used in

CW by assessing changes in the 1991-1993 policy that simultaneously implemented

the HITC and expanded the EITC, compared to 1989-1990. This strategy estimates

the eﬀect of the HITC combined with the EITC by comparing the average change in

the outcomes for the treatment group with that of the control group.6 As in CW,

my treatment group is working single mothers not exceeding a high school education

and the control group is working single women (without children) not exceeding a high

school education.

My primary outcome of interest, private health insurance coverage, is based on

the following SIPP questions: (1) ‘Was the respondent covered by a private health

insurance plan speciﬁcally under her own name?’ (2) ‘Was this individual-type plan

covering only the respondent?’

(3) ‘Was this family-type plan covering all of the

children in the respondent’s family?’

Single women without children (the control group) are deﬁned as covered if they

answered ‘yes’ to the ﬁrst two questions. Single mothers with children (the treatment

group) are deﬁned as covered if they answered ‘yes’ to the ﬁrst and third questions.7

5For example, if annual income was between $1 and $7,140, the credit was 6 percent of income. If one’s
income was between $7,140 and $11,250, the credit stayed constant at $428. The credit gradually decreased
to zero at the income-level of $21,250. The average amount received by HITC-qualiﬁed individuals was about
23 percent of the overall average cost for health insurance premiums (GAO, 1994).

6The DD assumes that the trend in outcomes for both groups would have been the same without the

1991-1993 policy. Therefore, any deviation from this trend is attributed to the 1991-1993 policy.

7One advantage of the SIPP is that it has information about the type of health insurance: individual or
family. Despite this, due to limitations of the data (e.g., in 1989, subsequent questions of health insurance only
asked whether it covers ‘all’ or ‘only the respondent’), I consider the treatment group to be covered only if her
family coverage accommodates ‘every child in her family.’ Therefore, the ﬁndings below may be conservative
estimates of the eﬀects of the HITC because mothers whose family plans only covered one of their children
might not be considered as covered.

3

In the baseline speciﬁcation, I use the same linear probability model as CW (OLS):

yist = β0 + β1 ∗ T reatist + β2 ∗ 1(t = 91, 92, 93)t+
β3 ∗ T reat ∗ 1(t = 91, 92, 93)ist + β4 ∗ Zist + it

(1)

where i, t and s index individual, time (year) and state, respectively. The outcome

variables of interest, yist, are binary variables indicating whether the individual [1] ‘was

covered by private health insurance under the respondent’s name,’ [2] ‘had visited a

physician at least once in the previous year,’ and [3] ‘had a health status that was

good, very good, or excellent.’ T reatist represents an indicator for a single mother.
1(t = 91, 92, 93)t is a dummy for the years 1991 to 1993. T reat ∗ 1(t = 91, 92, 93)ist is

equal to unity only if she was in the treatment group and the tax year is 1991, 1992

or 1993. The estimate of β3 denotes the eﬀect of the 1991-1993 policy, the combined

eﬀect of the HITC and the EITC. Zist includes same controls as used in CW.8

Although estimating (1) provides useful information about the HITC combined

with the EITC, β3, I wish to estimte the eﬀect of the HITC in isolation of the EITC.

While CW also extends their analysis to isolate the HITC eﬀect, their Diﬀerence-in-

Diﬀerence-in-Diﬀerences (DDD) does not work with my data.9 Instead, I conduct a

diﬀerent DDD by further including the information from 1994 to 1995 when the HITC

was repealed and the EITC was expanded again.10 Including the additional information

8This includes race, age, categories of monthly total earned income that are converted to 1989 dollars
(<$500, $500-$1000, $1000-$1500, $1500-$2000, >$2000), work status (Full-time/Full-month, Part-time/Full-
month, Full-time/Part-month, Part-time/Part-month) and number of children in the household. I also control
for state-ﬁxed eﬀects, state unemployment rates (U RTst) and the interaction of (U RTst) with the treatment
group indicator.

9In the SIPP, the main questionnaire was changed before and after 1989 (e.g., the SIPP explicitly asked,
“whether a respondent has private health insurance” in 1989 onwards, whereas it asked more generally,
“whether a respondent has health insurance” before 1989).

10Congress passed the OBRA of 1993 with an enactment of the largest EITC expansion in history (e.g., a
mother with one child could receive a maximum credit of $1434 in 1993, while the maximum credit increased
to $2038 in 1994).

4

from 1994 to 1995 enables me to net out the possible inﬂuence of the EITC. Speciﬁcally,

I estimate the model below:

yist = δ0 + δ1 ∗ T reatist + δ2 ∗ 1(t = 91, 92, 93)t+
δ3 ∗ 1(t = 94, 95)t + δ4 ∗ T reat ∗ 1(t = 91, 92, 93)ist+
δ5 ∗ T reat ∗ 1(t = 94, 95)ist + δ6 ∗ Zist + it

(2)

The only change in (2) is that 1(t = 94, 95)t and T reat ∗ 1(t = 94, 95)ist are now

included.11 While δ4 estimates the change in coverage among single mothers from

1991 to 1993, relative to 1989-1990, δ5 estimates the change in coverage among single

mothers from 1994 to 1995, relative to 1989-1990. With an additional assumption that

the 1994-1995 EITC expansion had the same impact as that of 1991-1993, the change
attributed solely to the HITC can be estimated as δ4 − δ5

2 .12

1.2.2 Data

I use data from the SIPP. Households are interviewed once every four months and

asked questions about the previous four months. Within each SIPP panel, the sample

is randomly divided into four rotation groups. One rotation group is interviewed each

month and after all rotation groups complete their ﬁrst interview, the ﬁrst wave of

the panel concludes. This continues typically for eight waves of each panel over the

11The sample now has 1989-1995 time frame.
12To see why this quantity is an estimate of the HITC only, denote the 1991-1993 EITC eﬀect on coverage
as a1, the HITC eﬀect on coverage as a2 and the 1994-1995 EITC eﬀect on coverage a3. Then, I can rewrite
δ4 = a1 + a2 and δ5 = (a1 + a2) + (a3 − a2). The ﬁrst term on the right-hand side (RHS) of δ5 is the eﬀect of
the 1991-1993 policy and the second term on the RHS represents the subsequent change in 1994-1995. With
an additional assumption that a1 = a3, I can rewrite δ5 = 2a1. Therefore, a2 = δ4 − δ5
2 measures the ‘HITC
eﬀect on coverage.’ All of this analysis is based on the assumption that the eﬀect of removing the HITC, −a2,
is the negative of the eﬀect of adding the HITC, a2.

5

course of three years.13 For each SIPP panel, I select a wave that represents each year

from 1989 to 1995. I use single women drawn from the third wave of the 1989 to 1993

panels (September to December for each year). Responses from SIPP Panel-1993 wave

6 and wave 9 represent periods from September to December in 1994 and September

to December in 1995, respectively.14 Table 1.1 provides the descriptive statistics of the

sample from 1989 to 1995.15

1.3 Results

1.3.1 Coverage Rates

Columns 2-3 in Table 1.2, representing results from (1), indicate that private health

insurance coverage was greater by about 7.1 pp than it otherwise would have been for

single mothers from 1991 to 1993.16 Even with a diﬀerent data set, my results are very

similar to that of CW that estimated an increase in coverage of about 4.7 pp due to

the 1991-1993 policy.17

In Table 1.3, I verify the robustness of the results. First, there were statewide

reforms [i.e., state Aid to Families with Dependent Children reforms (AFDC) and

state-speciﬁc EITCs] that might have confounded the results. Since state AFDC re-

13Multistage-stratiﬁed sampling is the other important aspect of the SIPP. To take this into account, I
report both the weighted (WLS) and unweighted (OLS) estimates of the linear regression analyses below in
Table 1.2 and 1.4. I only report the weighted estimates for the remaining tables.

14I use 6th and 9th interviews of individuals from SIPP-1993 Panel to examine the HITC repeal along with

the EITC expansion in 1994-1995 as there was no new sample collected during these years.

15Table 1.9 in the appendix shows the changes in outcome variables of interests during this period.
16If I take the number of the HITC eligible families headed by working single mothers with low education
from the 1991 CPS (i.e., 2,485,000) and the estimated coverage increase of about 7.1 pp, there would be an
increase in enrollment by about 176,435 people who would have otherwise not enrolled in health insurance.

17In addition to this, Table 1.6 in the non-published appendix shows the event history analysis where I dis-
aggregated the HITC combined with the EITC eﬀect by years to explore whether this had a similar magnitude
in all three years. Further, leaving out the interaction term of 1989 and the treatment dummy, there was no
signiﬁcant pre-treatment eﬀect in 1990, possibly supporting the validity of the common trend assumption.

6

Table 1.1: Summary Statistics, 1989-1995

Single Women Single Mothers

30.9
(7.93)
.168
(.374)
.831
(.374)
-

.833
(.372)
.136
(.343)
.029
(.170)
.801
(.398)
.168
(.374)
.019
(.137)
.010
(.102)
1,254
(881)
6.24
(1.40)

.634
(.481)
.704
(.456)
.917
(.275)
2,279

30.3
(7.90)
.230
(.420)
.769
(.420)
1.86
(1.04)
.755
(.430)
.220
(.414)
.024
(.155)
.729
(.444)
.231
(.422)
.022
(.149)
.015
(.123)
1,123
(713)
6.22
(1.35)

.128
(.334)
.671
(.469)
.916
(.276)
4,216

Variables

Age (in years)

% w/<12 years of education

% w/=12 years of education

Number of Kids

% White

% Black

% Others

% Full-time, Full-Month

% Part-time, Full-Month

% Full-time, Part-Month

% Part-time, Part-Month

Total Income (Monthly $
At the time of the interview)
% Unemployment Rate in one’s State

Private Health Insurance under own name-covered

Annual Oﬃce Visit (Extensive Marign; Any)

Self-Reported health good/very good/excellent

Observations

7

Table 1.2: Estimates from Equation (1), 1989-1993

Covered by Private Health Insurance

(1)

(2)

(3)

Treat, β1

1(t=91,92,93), β2

Treat*1(t=91,92,93), β3

State FE
Observations
R-squared

CW (2014) WLS

OLS

-.128***
(.024)
-.142***
(.001)
.047***
(.012)

Y
21,152
.336

-.472***
(.072)
-.079**
(.032)
.071*
(.038)

-.468***
(.069)
-.091***
(.029)
.081**
(.032)

Y
4,722
.391

Y
4,722
.382

Table 1.3: Robustness Check, 1989-1993

Covered by Private Health Insurance

(1)

(2)

(3)

Treat

1(t=91,92,93)

Treat*1(t=91,92,93)

-.409***
(.057)
-.103***
(.033)
.080*
(.044)

-.487***
(.081)
-.078**
(.036)
.059
(.042)

-.454***
(.068)
-.083**
(.036)
.072*
(.040)

Excluding states that adopted welfare waivers
Excluding states that had state-level EITCs
Including an indicator for high school graduates
State FE
Observations
R-squared

Y

Y
3,573
.389

Y

Y
4,328
.387

Y
Y
4,722
.340

8

forms restricted the duration of welfare reliance, it resulted in eligibles getting into the

labor force, often accompanied by health insurance. Therefore, I exclude states that

instituted an AFDC reform and re-estimate (1). The result in column 1 of Table 1.3

was similar to Table 1.2, suggesting that the coverage increase was not mainly due

to AFDC reforms. Because state-EITC beneﬁts could also provide another source of

variation for the impact of tax credits on coverage (Baughman, 2005), I exclude states

that had their own speciﬁc-EITC beneﬁts. The result in column 2 remains unchanged,

thereby showing that state-speciﬁc EITCs are not a signiﬁcant concern. With reference

to Eissa and Hoynes (2006) that respondents might adjust their income to be eligible

for the HITC, column 3 addresses this concern by re-estimating (1) without income

being included.18

18While I exclude income controls, I do consider education-level in column 3. Table 1.7 and Table 1.8 in
the non-published appendix analyze two additional robustness checks. They assess whether the increase in
private coverage is shifting either from the uninsured population or from the Medicaid enrollees. Both Tables
1.7 and 1.8 oﬀer evidence that the combined eﬀect of the HITC and the EITC from 1991 to 1993 was a result
of the uninsured population obtaining private coverage.

9

Table 1.4: Estimates from the Equation (2), 1989-1995

Private Health Insurance

(1)

(2)

(3)

OLS

(4)

WLS

(5)

OLS

HITC alone (1985-1993 sample)
a2 = δ4 − δ5

2

Treat, δ1

1(t=91,92,93), δ2

1(t=94,95), δ3

Treat*1(t=91,92,93), δ4

Treat*1(t=94,95), δ5

CW (2014) WLS
.036***
(.011)

.058**
(.027)
-.473***
(.048)
-.079***
(.029)
-.037
(.025)
.070*
(.034)
.024
(.030)

.061***
(.022)
-.475***
(.047)
-.093***
(.025)
-.047*
(.023)
.081***
(.028)
.038
(.026)

.062**
(.027)
-.441***
(.045)
-.090***
(.032)
-.050*
(.028)
.078**
(.036)
.031
(.033)

.067***
(.022)
-.445***
(.045)
-.104***
(.028)
-.059**
(.026)
.092***
(.028)
.050*
(.029)

Income
High school graduates

Y

Y

Y

Y

Y

State FE
Observations
R-squared

Y
26,796
.328

Y
6,495
.395

Y
6,495
.385

Y
6,495
.351

Y
6,495
.345

In an eﬀort to isolate the HITC, Table 1.4 suggests that the HITC eﬀect (a2 =

δ4 − δ5

2 ) is about 5.8 pp based on estimates from (2). Given the aforementioned DDD

assumption, I conclude that about eighty percent (5.8/7.1) of the 7.1 pp increase in

coverage of single mothers was associated with the HITC only, just as CW attributed

three-quarters (3.6/4.7) of the 4.7 pp increase to it.19

19Here, I am treating the EITC-expansion eﬀects, a1 (1991-1993) and a3 (1994-1995), as identical. However,
as the EITC expansion in 1994 was larger than in 1991 (e.g., in 1994 the maximum EITC increased by 42.1%
while in 1991 it increased by 25.1%), it might be more reasonable to relax the assumption as a3 ≥ a1 ≥ 0. If
so, the bounds on the HITC eﬀect, a2, would be (δ4 − δ5

2 , δ4), which is (5.8, 7.0) pp.

10

1.3.2 Health-Care Utilization and Health Status

Using (1) with utilization as an outcome variable, columns 1-2 in Table 1.5 show the

eﬀect of the HITC along with the EITC on the probability of an oﬃce visit.20 Columns

5-6 make use of the question regarding self-reported health to construct a binary mea-

sure for the outcome variable that represents a ‘good, very good, or excellent health

status.’21 To disentangle the HITC eﬀect only, I re-estimate (2) and the corresponding

results can be found in columns 3-4 and 7-8.

20I deﬁne utilization as a physician’s oﬃce visit at least once per year that represents the extensive margin
eﬀects on health-care demand. The primary reason for this is that the frequency of utilization could be
confounded with the individual’s health status, leading to biased estimates of the HITC along with the EITC
eﬀect on health-care utilization (Currie and Gruber, 1996). One way to mitigate this concern is explicitly
focusing on preventive care (e.g., an oﬃce visit for a routine check-up that is recommended once a year).
In other words, an absence of an oﬃce-visit per year suggests an inaccessibility to the health-care system,
regardless of health status.

21Refer to notes under Table 1.5 for additional details.

11

Table 1.5: Health-Care Utilization & Self-Reported Health Status

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

T.

1(t=91,93)

1(t=94,95)

T.*1(t=91,93)

T.*1(t=94,95)
a2 = δ4 − δ5

2

Oﬃce Visit
(Extensive Margin; %)
Eq.(1)
.056
(.086)
.039
(.043)

.054
(.086)
.038
(.043)

.026
(.049)

.026
(.050)

Eq. (2)
-.039
(.076)
.053
(.041)
.007
(.040)
.0003
(.044)
.077*
(.041)
-.038
(.041)
Y

-.033
(.076)
.051
(.041)
.002
(.038)
.002
(.045)
.081*
(.040)
-.038
(.042)

Y

Health: good/very good
/excellent
Eq. (1)
.061
(.052)
-.059***
(.020)

.059
(.051)
-.063***
(.020)

.065***
(.021)

.068***
(.022)

Y

Eq. (2)
.033
(.049)
-.053***
(.019)
-.045***
(.027)
.056***
(.020)
.021
(.034)
.046***
(.016)
Y

Y

Y
3,668
.047

Y
4,563
.042

.034
(.049)
-.057***
(.019)
-.049***
(.028)
.060***
(.021)
.025
(.035)
.047***
(.017)

Y

Y
4,563
.046

Income
High school.

Y

Y

State FE
Obs.
R-squared

Y
3,668
.044

Y
3,668
.038

Y
4,563
.038

Y
4,563
.034

Y
3,668
.042

Overall, Table 1.5 displays that gaining private coverage did not translate into

a signiﬁcant increase in oﬃce visits, but it might have improved single mothers’ health

status by about 4.6 pp.22 This is consistent with recent ﬁndings on whether the coverage

expansion under the ACA has aﬀected health status.23 As the likelihood of having ‘at

least one annual oﬃce visit’ is not the only dimension to measure utilization, if there

were more thorough measures, it would have been helpful to see the reason for improved

health status during 1991-1993.24

22Since the economy suﬀered a recession in the early 1990s, it might be plausible that the general population
experienced worsening health status as its consequence (Ruhm, 2000). Interestingly, Table 1.5 results indicate
that the HITC might have mitigated this degrading trend.

23After the ACA’s coverage expansion, there was an improvement in self-reported health status (Sommers

et al., 2015; 2017).

24One possible mechanism might be, as a result of the coverage, people in the treatment group were more

likely to have a primary doctor.

12

1.4 Conclusions

For decades, disagreement over health-care policy has been a major concern, and if any-

thing, that concern has grown with the enactment and potential repeal of the ACA.

Given this, I revisit the eﬀects of the HITC, the tax credit policy passed in the early

1990s, to provide a better evidentiary base for the usefulness of tax credits.

My estimates substantiate the ﬁndings of CW that the implementation of the

HITC with the EITC increased the coverage by 7.1 pp. Also, I ﬁnd that coverage was

increased by 5.8 pp solely due to the HITC. These estimates are based on a data set

distinct from CW, and as for isolating the HITC, a distinct strategy is constructed

based on the HITC repeal and the EITC expansion. Although it was a signiﬁcant in-

crease, a magnitude of 5.8 pp shows that the HITC was not large enough to encourage

everyone to be insured. Even with the HITC and the EITC in place simultaneously,

the uninsured rate was still around 16.4 % in 1991-1993 (Cohen et al., 2009), implying

that achieving universal health-care by only tax-credit schemes will be challenging.25

Moving beyond health insurance, my results indicate that the HITC improved

self-reported health. This suggests that for low-income families, the inability to ac-

quire coverage might be the primary barrier for improved health status. Considering

all ﬁndings of the HITC, making tax credits available for low-income families, a rela-

tively inexpensive mechanism to implement, can be eﬀective to provide incentives for

coverage take-up and to achieve better health (albeit, if appropriate regulations were

enforced). With that said, the ultimate repeal of the HITC validates the fact that it

25A possible explanation for this small magnitude is that the modest amount of tax credits, relative to high
premiums, was insuﬃcient to incentivize eligible individuals to enroll in those beneﬁts (GAO, 1994). The other
possible explanations would be insuﬃcient outreach and lack of publicity regarding the HITC. This problem
is also documented with the ACA exchanges, as about half a million fewer people signed up for insurance in
2017. This number would have been higher with an equal level of publicity under the Obama Administration.

13

could have been more eﬀective if the appropriate regulations had been in place.26 As

the U.S. is at the cusp of policy reforms, this paper has provided timely insights into

the various aspects of tax credits.

26Even when the market was mostly unregulated, the HITC still resulted in an increase of the coverage
and improved health status in 1991-1993. However, the HITC did not specify minimum beneﬁts that must be
included in insurance plans (as in a recent replacement proposal—AHCH includes a clause about removing 10
Essential Health Beneﬁt mandates), enabling insurance companies to sell valueless plans to tax-credit eligible
candidates (Sanger-Katz, 2017). This ultimately resulted in its repeal despite the relative success.

14

APPENDIX

15

Event history analyses for the 1991-1993 policy regime

This table below oﬀers additional evidence for Table 1.2 by showing that there was

no signiﬁcantly diﬀerent pre-trend in 1990. This also shows that the estimated eﬀect

of the HITC along with the EITC had the similar magnitude in all three years, 1991,

1992 and 1993.

Table A.1: Event History Analyses, 1989-1993

Private Health Insurance coverage

Treat

Treat* I(t=89)

Treat* I(t=90)

Treat* I(t=91)

Treat* I(t=92)

Treat* I(t=93)

State FE
Observations
R-squared

(1)
WLS
-. 477***
(.091)
-

(2)
OLS
-.473***
(.089)
-

.032
(.050)
.095
(.065)
.112**
(.047)
.068
(.051)

Y
4,722
.390

.025
(.046)
.109*
(.062)
.124**
(.045)
.076*
(.044)

Y
4,722
.338

Additional robustness-check for uninsured coverage rates

This section answers the question that may arise whether or not an increase in private

coverage in 1991-1993 was from the uninsured population. To do this, I re-estimate

equation (1) in the main text by replacing the outcome variable with an indicator for

having neither private nor public coverage. The results below display that the eﬀect on

un-insured rates (-7.3 pp) was about the same size (with a negative sign) as the eﬀect

16

on private coverage in Table 1.2 (7.1 pp). This supports the idea that the increase in

private health insurance coverage from 1991 to 1993 mostly came from the uninsured

population.

Table A.2: Change in Uninsured Coverage Rates, 1989-1993

Uninsured

Treat

I(t=91,92,93)

Treat* I(t=91,92,93)

State FE
Observations
R-squared

(1)
WLS
-.105**
(.049)

(2)
OLS
-.124**
(.050)

.039
(.034)

.041
(.031)

-.073**
(.031)

-.060*
(.030)

Y
4,722
.142

Y
4,722
.142

Additional Robustness Check for Change in Coverage among Medicaid En-

rollees

Due to the concern that private health insurance coverage might have arisen from

Medicaid enrollees switching their coverage, I use an additional individual ﬁxed eﬀects

(FE) estimation strategy with the following equation:

yist = β0 + β1 ∗ T reatist ∗ 1(t = 91, 92)t + β2 ∗ Zist + it

(3)

By taking advantage of the panel nature in the SIPP, I track the changes in coverage

among Medicaid enrollees at the beginning of their interviews. Through the SIPP-1990

Panel which covers 1990 to 1992, I try to get a conclusive result whether the Medicaid

17

enrollees changed to private health insurance in 1991 and 1992. In the above equation,

the estimate of β1 is my primary interest. Corresponding results in Table 1.8 do not

have any statistical signiﬁcance. This suggests that the possibility of being overstated

due to the change in coverage among Medicaid enrollees would not be an issue.

Table A.3: Private Coverage among Medicaid Enrollees, 1990-1992

Private Health Insurance Coverage
Treat*(t=91,92)

(t=91)

(t=92)

Observations
R-squared
Number of Individuals

(1)
-.071
(.063)
.051
(.059)
.056
(.064)

742
.083
106

(2)
-.042
(.047)
.022
(.043)
.028
(.052)

742
.088
106

18

Table A.4: Coverage Rates, Oﬃce Visit and Health-Status Report

1989

1990

1991

1992

1993

1994

1995

Total

.148
(.355)

.139
(.346)

.133
(.340)

.122
(.327)

.128
(.334)

.115
(.320)

.114
(.318)

Outcome
Single mothers
Insurance that
covers children

Oﬃce Visit (Any)

Health:good/very-good .922
excellent

(.267)

.919
(.273)

.919
(.273)

.640
(.480)

.670
(.469)

.655
(.475)

-
-

-
-

.670
(.470)

.711
(.453)

.926
(.260)

.894
(.307)

-
-

-
-

Obs.
Single Women
Insurance

439

889

458

672

601

579

578

4216

.700
(.459)

.669
(.470)

.608
(.489)

.570
(.495)

.628
(.484)

.642
(.480)

.633
(.482)

Oﬃce Visit (Any)

.695
(.461)

.726
(.446)

.677
(.468)

Health:good/very-good .950
excellent

(.218)

.927
(.259)

.891
(.311)

-
-

-
-

.719
(.449)

.686
(.464)

.917
(.275)

.901
(.297)

-
-

-
-

Obs.

220

457

276

382

328

316

330

2279

19

Chapter 2. The Eﬀects of the Dependent Health Insurance

Coverage Mandates on Fathers’ Job Mobility and Compensa-

tion

2.1 Introduction

Historically, young adults aged 19–25 experienced lower health insurance coverage rates

than other groups. The main reasons for this might be that (1) young adults are gen-

erally healthy so they may perceive less need for health insurance, and (2) they often

work in entry-level jobs that are less likely to provide health insurance (Barkowski and

McLaughlin, 2018). The alternative to employer-provided health insurance (EPHI) is

enrollment in a non-group plan, which can be too expensive for young adults given

their generally lower income compared to that of other working-age groups. Because of

these factors, young adults may forego purchasing health insurance. Seeking to increase

health insurance for this young adult population, both state and federal policymakers

mandated that health insurance companies expand the age that children could remain

covered under their parents’ health insurance.

Although many studies ﬁnd positive eﬀects of these mandates on young adults’

health insurance coverage rates (Levine et al., 2011; Dillender, 2014; Cantor et al.,

2012; Akosa Antwi et al., 2013), the literature lacks studies detailing the implications

for the parents of those young adults. Because the mandates increased the value of

jobs with EPHI for parents who had eligible children, parents’ job mobility could be

constrained. Understanding such potential eﬀects is important because middle-aged

workers (aged 45–64) are in the prime earning years of their careers.

20

Speciﬁcally, the mandates might limit the job choices for parents because they

could provide a more comprehensive and relatively cheaper insurance plan as a valu-

able safeguard for their adult children’s health and ﬁnancial security while promoting

their children’s career progression.27 Thus, the mandates might increase the parents’

cost of leaving an employer with EPHI compared to the time period prior to the im-

plementation of the mandates. I, therefore, expect that workers could be less likely

to leave their jobs when their children were eligible for dependent coverage mandates.

Conversely, for parents without EPHI, these mandates made their then-current state

of employment less attractive; as such, I expect that these people could be more in-

clined to pursue jobs with EPHI. Consequently, this research addresses the extent to

which the state and federal dependent health insurance mandates caused fathers to

experience job-lock and job-push, that is, respectively, remaining in their jobs for fear

of losing EPHI and seeking out jobs with EPHI that they would otherwise not have

chosen.

In addition to highlighting the unintended consequences that accompanied the

mandates, this paper further contributes to the literature in two important ways. First,

this paper exploits the state and federal mandates together, as suggested by Barkowski

and McLaughlin (2018). Examining state and federal mandates in tandem is important

because they had a shared primary objective of increasing coverage among young adults

and had similarities in the eligibility criteria. Second, this research uses a comprehen-

sive dataset (the combination of survey and administrative data) to examine whether

27Given that health insurance enrollment decisions in the United States were often made at the immediate-
family level as opposed to the individual level (Cutler and Gruber, 1996), covering dependents through parental
coverage is a cost eﬀective decision. Brandeisky (2015) shows that, in 2015, an individual premium cost an
average of $486 a month for young adults. By adding two or more dependents to the parents’ plan, however,
a health insurance premium cost an average of $1,377 a month, thus lowering the cost per individual.

21

the implementation of the mandates caused a decrease in annual earnings or other

types of compensation. This decrease could occur because the mandates increased the

relative costs for employers to hire those parents with eligible adult children.28

I observe that working fathers with eligible children experienced a 42 percent

decrease in the likelihood of voluntary separation from employers providing EPHI. My

results also provide weak evidence suggesting that fathers who decided not to sepa-

rate from such employers in the current wave could experience a modest reduction in

earnings.29 Taken together, all of these ﬁndings about the potential eﬀects on parents

would allow for a holistic understanding of the mandates’ eﬀects.

The following section explains the institutional details of the dependent cover-

age mandates. Section 3 presents the literature review and Section 4 describes the

methods. Section 5 discusses my results, and Section 6 concludes this paper.

2.2 Institutional Details

Before the dependent coverage mandates required insurance providers to extend the

age limit for dependents, most public health plans (e.g., Medicaid and CHIP) and

private health plans (e.g., self-insured EPHI, EPHI through an insurance company, or

plans through the non-group market) removed young adults from their parents’ po-

lices.30 This most commonly occurred when they turned 19 unless they were enrolled

in a college or university as a full-time student. If a dependent was a full-time student,

then he or she was typically covered through the age of 22. This left many young adults

28In 2012, the average employer contribution for employees’ family plans was about 73 percent or about
$ 11,429 (The Kaiser Family Foundation, 2017). As the dependent children were covered under the family
plan, the ﬁnancial burden of the insurance premium and health care cost could be transferred not only to the
parents, but also to their employers (Chen, 2018).

29As explained further in the data section, each wave is a four-month period.
30The dependent, in this case, referred to biological or legally fostered children.

22

uninsured if they were not currently attending college. Moreover, in some states, the

tax code deﬁned coverage of dependents (19 years of age or older) as a taxable beneﬁt,

deterring parents’ employers from extending coverage to their adult children. These

factors contributed to 31 percent of young adults being uninsured in 2009, which equals

approximately 9.2 million people between the ages of 19 and 25 (Busch et al., 2014).

To increase health insurance coverage for this young adult population, state pol-

icymakers expanded access to dependent coverage. In the absence of state funds to

expand public programs, many states required ﬁrms to oﬀer dependent coverage as

part of their plans for increasing the age threshold, generally up to 23–25 years of age

(Goda et al., 2016). By 2010, 30 state-level dependent coverage expansions were in

eﬀect (see Table 2.9).31 Because of the state-level mandates, the dependent coverage

rate increased by approximately 11.9 percent (Burgdorf, 2014; Monheit et al., 2011).

Following the states’ lead, the federal government enacted the dependent cover-

age expansion through the 2010 Aﬀordable Care Act (ACA), which required insurers

to expand coverage to children up to the age of 25 on their parents’ plans. Whereas

some state mandates limited eligibility based on factors other than age, the federal

law was straightforward: any insurance plan that already oﬀered dependent coverage

must oﬀer the same level of beneﬁts at the same price to dependents 25 years of age

or younger.32 Furman and Fiedler (2015) ﬁnd that due to the federal mandate, the

31While almost all states with state-level mandates expanded their eligibility to 23–25 years of age, some
states extended the provision to age 29 (i.e., New York, New Jersey and Pennsylvania) and other states
extended an indeﬁnite age of eligibility (i.e., Iowa and Texas). Some states also required student status, single
marital status or ﬁnancial dependency to be qualiﬁed as a dependent. Beyond the diﬀerences in eligibility
among dependents, the parents with EPHI from self-insured ﬁrms were exempt from the state mandates under
the Employee Retirement Income Security Act of 1974. Lastly, most states did not regulate the employee-paid
premiums that could be levied for coverage of older dependents, potentially allowing ﬁrms to raise prices above
what employees could aﬀord.

32The federal mandate did not depend on co-residence with parents, student status, marital status or
ﬁnancial dependency. It applied to all insurance plans including self-insured EPHI, fully-insured EPHI and
plans from the non-group market.

23

uninsured rate among young adults dropped by more than 40 percent from 2009 to

2014, which translates to 4.5 million additional young adults with coverage.33 Cantor

et al. (2012) note that the federal mandate was a “rare public policy success in the

eﬀort to cover the uninsured [young adults].”34

2.3 Literature Review

A large body of empirical literature exists regarding job-lock. The majority of em-

pirical and anecdotal evidence suggests that mobility constraints in the labor market

stem from the fear of losing health care coverage.35. For instance, Rashad and Sarpong

(2008) ﬁnd that individuals with EPHI were 60 percent less likely to voluntarily leave

their jobs compared to those receiving insurance elsewhere. Most job-lock studies rely

on the idea that a worker’s demographic characteristics—such as proximity to retire-

ment or health status—might lead him or her to value insurance more highly than

others, making that worker more vulnerable to job-lock (Kapur and Rogowski, 2007;

Blau and Gilleskie, 2001; Bradley et al., 2005). Compared to the abundant literature

about job-lock, fewer researchers study job-push, and one example of such studies sug-

gests that EPHI encouraged some workers to leave jobs that are otherwise desirable

(Anderson, 1997).

There is a considerable amount of literature about the state and federal man-

dates that focus on decreasing uninsured rates and job-lock for young adults (Levine et

33These gains alleviated more than two-thirds of the gap in uninsured rates between young adults and other

non-elderly adults (Furman and Fiedler, 2015).

34There is one caveat that is worth noting: this coverage extension often did not work well for young
adults living out-of-state because their parents’ plan might only provide expensive, out-of-network coverage
(Goldman, 2013; Reinicke, 2018).

35Some ﬁndings in the literature, however, suggest that there is little evidence of job-lock phenomenon

(Gilleskie and Lutz, 2002; Kapur, 1998)

24

al., 2011; Monheit et al., 2011; Cantor et al., 2012; Antwi et al., 2013; Sommers et al.,

2013; Colman and Dave 2017; Kofoed and Fraiser, 2019). Most papers in the literature,

however, study state- and federal-level mandates independently. For example, Antwi

et al. (2013) and Cantor et al. (2012) only discuss the federal mandate; they jus-

tify omitting the eﬀects of the state mandates by arguing these eﬀects were negligible.

Yet, including the eﬀects of the state mandates is necessary given the impacts of both

the state and federal mandates on various outcomes such as young adults’ insurance

rates, marriage rates and educational attainment (Barkowski and McLaughlin, 2018;

Gamino, 2018; Barkowski et al., 2018).

Despite the plethora of papers regarding the eﬀects of the dependent coverage

mandates on young adults, few researchers consider other populations. There is only

one paper that studies the eﬀects of the dependent coverage mandates on parents’

retirement decisions (Biehl et al., 2018), but this paper relies solely on the federal

mandate for identifying variation by using the Health and Retirement Study (HRS)

data. It is also limited by only considering retirement decisions without analyzing other

types of voluntary job separation.

Even though little prior work explicitly investigates the link between the depen-

dent coverage mandates and parents, there is some evidence that mandates related to

child health insurance aﬀected parents’ voluntary job separation. For instance, Chat-

terji et al. (2016) ﬁnd that the prohibition of the pre-existing condition exclusions

for children increased the likelihood of leaving an employer voluntarily by 37 percent

among fathers of disabled children relative to fathers of healthy children. Barkowski

(2017) also ﬁnds that Medicaid eligibility for household members (especially for eligible

25

children) increased the probability of a voluntary job separation by 34 percent among

working fathers with EPHI. Hamersma and Kim (2009) ﬁnd that Medicaid decreased

job-push, suggesting that unemployed fathers or working fathers without EPHI felt

less need to move to jobs that oﬀer insurance. As a caveat, Barkowski (2017) and

Hamersma and Kim (2009) focus on low-income workers, and Chatterji et al. (2016)

investigate job mobility of parents with disabled children. Since both studied groups

might be systematically diﬀerent from the general group of middle-aged fathers, a more

comprehensive approach for this group merits discussion.

In addition to job mobility, several papers examine whether health-beneﬁt re-

lated mandates inﬂuenced eligible workers’ annual earnings or other types of compen-

sation as these mandates raised the relative cost for ﬁrms to insure their workers. This

exploration is critical since the eﬃciency of these mandates largely depended on the

extent to which their costs were shifted to group-speciﬁc wages (Gruber, 1994).36 In

spite of several regulations (e.g., non-discrimination laws) that prevented these shifts,

Gruber (1994) ﬁnds a substantial shift in the costs of the group-speciﬁc mandate to

the wages of the targeted group. This study inspired subsequent articles seeking to

determine the eﬀects of health insurance mandates on earnings.37 Alternatively, co-

workers might share the cost of providing additional insurance. A study by Goda et

al. (2016) suggests that the wage reduction of employees (including those who did not

beneﬁt from the mandates) could range from $30 to $1,500 per worker depending on

36In examining the eﬃciency of group-speciﬁc mandates, a central consideration is whether the cost of the
mandate was shifted to the wages of the group that beneﬁted. Without the ability to adjust wages accordingly,
there might be substantial deadweight loss from these mandates even if the beneﬁt was valued by the group
(Gruber, 1994).

37Monheit and Rizzo (2007) review the relevant literature regarding the costs of various mandates for

employees and employers.

26

the number of coworkers sharing the costs.38

2.4 Methods

2.4.1 Data

In my analysis, I include married fathers between the ages of 45 and 64 with a youngest

child between the ages of 19 and 29, but I exclude fathers with a youngest child aged

26—the cutoﬀ age for the federal mandate. This is because the adult children’s exact

dates of birth are unknown and it is unclear whether they were treated by the man-

dates.39 Moreover, this sample excludes responses from states that had no age limit

and states that extended the provision to age 29. Among family units, I only focus on

fathers because they have more persistent attachment to their jobs than mothers. That

being said, the wage-labor supply elasticity of fathers is often much smaller than that

of mothers (Blundell and MaCurdy, 1999).40 Finally, one of my sample selection cri-

teria is based on the youngest child because fathers have an incentive to secure health

insurance for their children until their youngest child acquires his or her own access to

health insurance.41

To assess the eﬀects of the dependent health insurance coverage mandates, I

38Despite the wage reduction caused by the dependent coverage mandates, Goda et al. (2016) do not ﬁnd

any evidence that suggests workers reduced their labor supply in response to lowered wages.

39I can only observe the year when the youngest child was born.

I, however, do not omit fathers with
children who were at the cutoﬀ age for the state mandates (generally less than or equal to 25) because they
received coverage through the federal mandate in later years. Additionally, I do not extend the child’s age
past 30 because adult children over 30 are systematically diﬀerent from adult children in their early 20s in
terms of life stage.

40In Appendix 4, I do the same analysis for mothers but do not ﬁnd any signiﬁcant changes in their labor
market outcomes caused by the mandates. This may be attributable to mothers’ expectation that they would
not remain in their jobs for a long time.
If true, this would suggest that they placed less value on the
beneﬁts provided by their companies and were less likely to be inﬂuenced by the mandates related to their
employer-provided beneﬁts.

41I use the youngest child to construct my samples, including the sample for job-push analysis. For the
job-push analysis, however, any child could aﬀect fathers’ job mobility decisions. So I also run the job-push
analysis based on the oldest child. This does not change my results.

27

leverage detailed information on individuals using the 2004 and 2008 Survey of Income

and Program Participation (SIPP) panels, which are linked to the Detailed Earnings

Records (DER) and Business Registrar (BR) data. The SIPP is a nationally repre-

sentative household survey. The time period covered in my data is January 2004 to

December 2012—when most state-level dependent coverage provisions and the federal

mandate were implemented. The entire sample is divided into four subsamples called

rotation groups. One rotation group is interviewed every 4 months, which hereafter is

called a wave. Most SIPP questions ask the respondent to report information regarding

the four months prior to the interview (United States Census Bureau, 2001).

I use the respondents’ health insurance, demographic characteristics and em-

ployment records from the core questions of every SIPP wave.42 The SIPP provides

a detailed set of information about current employment for up to two jobs in a given

wave. I only include the job that is considered the ‘primary job’—the job in which

the individual worked the most hours. The data provide the main reasons that fa-

thers left employers within this wave, if applicable, which allows me to separate vol-

untary versus involuntary job separation.

In my analysis, I focus on voluntary job

separation—transitioning between jobs, becoming unemployed, leaving the labor force

or transitioning from working for an employer to self-employment.43

Although the SIPP provides detailed, self-reported demographic characteristics,

the linked dataset between the SIPP and administrative records on earnings—DER

and BR—provides highly accurate measures of earnings and total monetary compen-

42None of the variables that I use are imputed.
43Involuntary job separation includes layoﬀs, childcare problems, family/personal obligations, illness/injury,
school/training, employer bankruptcy/change in ownership, termination of a temporary job, and unsatisfactory
work conditions.

28

sation. To construct this combined dataset, I ﬁrst link the respondents’ information

from the SIPP to the DER, which includes their W-2 information such as wages and

employer contributions to retirement beneﬁts.44 This SIPP-DER linked data can be

extended with BR data based on the EIN information available in the DER. The BR

data includes information like type of ﬁrms (i.e., single-unit or multi-unit) and the

parent company for all companies in the United States.45 The SIPP-DER-BR data

allows me to identify whether some respondents with two or more W-2s worked for

the same parent company and to calculate the total compensation from their primary

jobs. In my analysis, about 49.8 percent of the sample had two or more W-2s on ﬁle.

Of these respondents, about 20 percent had W-2s from the same parent companies.

Linking SIPP data with the administrative data, therefore, enables a comprehensive

understanding of the compensation adjustments caused by the mandates.46 Earnings

and other monetary compensation are inﬂation-adjusted using the yearly CPI-U in-

dices and by deﬁning 2012 as the base year.

Although most SIPP questions involve asking the respondent to report infor-

mation for each of the four months prior to the interview month, I only include the

responses from the interview month in order to mitigate seam bias.47 This means that

the analysis is conducted at the father-wave level rather than the father-month level.

To code the eligibility criteria for the mandates, I compile the data regarding

44The SIPP-DER linkage is only available until the end of 2012 through the United States Census, so the
responses for 2013 from the 2008 SIPP panel cannot be included in the analysis. While combining these
datasets, I also omit respondents who did not have Social Security Numbers.

45Firms themselves sometimes change or have multiple EINs for tax purposes or for multiple locations.
46Bridges et al. (2003) ﬁnd substantial measurement error in SIPP wage data. They conclude that the
mean SIPP wages were understated by 7.5 percent relative to the DER wages. Gottschalk and Huynh (2005)
also suggest that respondents with SIPP information but without DER records had lower earnings than
respondents with observed earnings in both data sets, possibly reﬂecting informal work arrangements.

47The seam bias is the tendency for respondents to report higher rates of events between survey waves than

within survey waves (Blank and Ruggles, 1996).

29

state laws (e.g., age limit and timing of implementation) from Depew (2015), Cantor

et al. (2012) and the National Conference of State Legislatures (2010). I demonstrate

the change in eligibility for fathers from three example states in the ﬁrst three rows in

Table 2.1. These states introduced state-level mandates before the federal mandate.

The last row in Table 2.1 presents the change in eligibility for fathers in states without

state-level mandates. I code the fathers in these states as eligible after September 2010

when the ACA was implemented.

Table 2.1: Examples of Childrens’ Age Eligibility by State

States Pre-State Law
Inelig.

Elig.

State Law Period

From 2010

Beginning Year Elig.

Inelig. Elig.

Inelig.

IN

Co

CT

MI

.

.

.

.

19–29

2008

19–23

24–29

19–25

27–29

19–29

2006

19–24

25–29

19–25

27–29

19–29

2009

19–25

27–29

19–25

27–29

19–29

.

.

19–29

19–25

27–29

In Table 2.2, I include the sample means for the outcome variables and covariates

for job-lock and job-push in two panels. For both panels, the columns titled Always

Ineligible contain the descriptive statistics for fathers who were not aﬀected by the

state and federal mandates. This is the intersection of the fathers whose youngest

child was ineligible across all time periods in Table 2.1. Ever Eligible is the group of

fathers who were aﬀected by the mandates at some point in my analysis. This is the

union of fathers, shown in Table 2.1, whose youngest child was eligible during any time

period from 2004 to 2012. Although Always Ineligible fathers within my sample were

30

generally older and were more likely to not have completed highschool, almost all other

characteristics are comparable to Ever Eligible.

For the job-lock analysis in columns 1 and 2 of Table 2.2, I include fathers who,

in the previous wave, were employed (but not self-employed) and had EPHI under their

own name. The sample includes approximately 11,500 working fathers, 71 percent of

whom had an Ever Eligible youngest child.48 The rate of voluntary job separation

within a 4-month wave, on average, is 1.7 percent. These rates are similar to those

reported in several papers based on SIPP data (Barkowski, 2017; Chatterji et al., 2016).

However, some other studies ﬁnd the rates that diﬀer from my rate of 1.7 percent. For

example, Bansak and Raphael (2008), shows that roughly 18 percent of workers with

EPHI separated from their employers within a year. This diﬀerence can be explained

by the fact that they consider all separations, not just voluntary ones.49

In columns 3 and 4 of Table 2.2, I include the fathers in the job-push sample

using the same selection criteria (e.g., their and their children’s ages) as those in the

job-lock sample. The only important diﬀerence is that the job-push sample includes

fathers who, in the previous wave, were unemployed or did not have EPHI from their

employers.50 Selecting the sample in this way limits the chance that job-push and

job-lock would be conﬂated since individuals without EPHI would not be aﬀected by

job-lock.

The last two rows in Table 2.2 provide the average total compensation and

48Due to the United States Census Disclosure rules, the total number of observations are rounded to the

nearest 500.

49Another diﬀerence is that I look for the job separation that happens within a wave, while Bansak and
Raphael use a between-wave measure for job-mobility. Further explanation for the within and between wave
measures in the SIPP can be found in Appendix A of Chatterji et al. (2016).

50Compared to those people in the job-lock sample in columns 1 and 2, the fathers in this job-push sample
were more likely to not hold a high school diploma, less likely to work in public sectors and less likely to
belong to a union. Thus, these fathers in this sample were not randomly selected.

31

Table 2.2: Descriptive Statistics of Fathers

Job-Lock Sample

Job-Push Sample

Always Inel. Ever Elig. Always Inel. Ever Elig.

.476
(.500)
52.9
(5.31)
.036
(.188)
.310
(.456)
.571
(.493)
.762
(.441)
.119
(.292)
.095
(.337)
.048
(.196)
.071
(.233)
.071
(.237)

.014
(.131)

2.10
10.3
(.997)
10.3
(1.02)

1.90

Variables

Eligible

Age

Highschool dropouts

Highschool graduates

Some college or higher

Non-hispanic white

African American

Hispanic

Asian and others

Public Sector worker

Union worker

Dependent Variables
Voluntary Job-
Separation rates

N. of Observation [1,000]
Ln(Annual Earnings
- in the DER)
Ln(Tot. Monetary Comp.
- in the DER)

-

56.2
(4.85)
.048
(.206)
.274
(.444)
.677
(.464)
.806
(.382)
.065
(.259)
.048
(.225)
.065
(.222)
.226
(.424)
.258
(.439)

.016
(.120)

3.10
10.9
(.725)
11.0
(.744)

.416
(.494)
53.2
(5.17)
.036
(.188)
.262
(.442)
.702
(.459)
.821
(.386)
.071
(.257)
.059
(.235)
.054
(.224)
.214
(.413)
.226
(.416)

.018
(.127)

8.40
11.0
(.785)
11.0
(.793)

-

56.6
(5.02)
.109
(.307)
.231
(.420)
.615
(.472)
.769
(.429)
.092
(.274)
.062
(.298)
.077
(.242)
.031
(.139)
.046
(.195)

.015
(.131)

0.65
10.1
(1.19)
10.2
(1.21)

N. of Observation [1,000]

3.00

8.20

0.55

32

annual earnings from linked SIPP-DER data.

2.4.2

Identiﬁcation Strategy

This study examines the eﬀects of both the federal- and state-level dependent coverage

mandates on fathers. The primary comparison is between two groups of fathers within

each state before and after the implementation of the mandates: those who had a

youngest child whose age is beneath mandate thresholds and those who had a youngest

child whose age is above mandate thresholds.

The model is speciﬁed as

yijt = β0 + β1 ∗ Eligijt + β2 ∗ Xit + β3 ∗ timet + β4 ∗ statej + ijt

(4)

where (4) is a diﬀerence-in-diﬀerences (DID) framework for individual i in state j and

at time (wave) t.51

To investigate job-lock where I only include fathers with EPHI in the previous

wave, the outcome variable—yijt—is set to one if a voluntary job separation happened

in the current wave. Because this is a binary outcome, I use a probit analog of equation

(4).52 Eligijt is the main independent variable and indicates whether fathers have

eligible children. It is determined by three things—state of residence, year of interview

and youngest child’s age—and for a given year, fathers are coded as eligible if they were

living in a state with a mandate in eﬀect and had a youngest child whose age was at or

beneath the mandated age. For instance, in the case of a father whose youngest child

51Because my sample consists of fathers who were at risk of leaving a job and the separation was observed
at most once for each father, my speciﬁcation is equivalent to a discrete time hazard model. Thus, it is not
possible to include individual ﬁxed eﬀects because there would not be enough variation remaining (Klerman
and Haider, 2004).

52This also applies to job-push analysis below.

33

was 24 years old living in Colorado in 2006, I would code him as eligible (Eligijt=1)

because Colorado enacted a dependent coverage mandate at that time. For another

father in Colorado in the same year but with a youngest child who was 25 years old, I

would code him as ineligible (Eligijt=0) because the child’s age exceeded the limit of

Colorado’s mandate.53 If fathers experienced job-lock, I would expect the coeﬃcient

of Eligijt, β1, to be negative.

Xit contains other covariates including father’s age and dummy variables. These

dummy variables are indicators of high-school dropouts, high-school graduates,

Black/Hispanic/Asian respondents, public sector workers and union workers. I include

full sets of state and year indicators, denoted with timet and statej, to focus on within-

state variation.54 In addition, I incorporate indicators for all the children’s ages from

20–29 (the indicator for 19-year-olds serves as the baseline group) to account for the

time-invariant behavioral diﬀerence of fathers with young adult dependents of various

ages.55

As one of the speciﬁcation checks, I also make use of the variation within state

and year that arose due to state and federal policy changes that broadened eligibility to

more age groups. I use this variation to examine whether fathers with children whose

age was near but above the maximum limit were aﬀected at the time when they should

not have been. To investigate this, I deﬁne a placebo group as part of the treated

group who had not been aﬀected by the state mandates but were eventually aﬀected

53Other requirements—most importantly, student status—are inappropriate to use for eligibility imputation
because they are jointly determined outcomes. For example, a state mandate might incentivize individuals to
pursue or terminate student status, so using it to determine eligibility would introduce bias (Depew, 2015).

54As a speciﬁcation check, I also examine whether including a linear state time trend would aﬀect my results.
55As mentioned, I do not include fathers with a 26-year-old child in the sample and so leave out their age

indicators in the regression.

34

by the federal one. To examine this, I consider the regression below.

yijt = β0 + β1 ∗ P laceboijt + β2 ∗ Eligijt + β3 ∗ Xit + β4 ∗ timet + β5 ∗ statej + ijt (5)

This equation compares the actual eﬀect of the policies across speciﬁc age groups

versus the placebo eﬀect, thereby making use of in-state age variation. Equation (5)

is developed based on the same criteria as equation (4): the child’s age, year and

state of residence. P laceboijt, is an indicator for the fathers whose youngest child was

slightly older than the age eligibility of the state mandate but still younger than that

of the federal mandate. 56 Eligijt is deﬁned in the same way as Eligijt in equation

(4) and captures the actual policy change of state and federal mandates. For example,

in Indiana, fathers with a youngest child aged 19–23 had been eligible under the state

mandate since 2008. In this state, therefore, Eligijt is equal to one for these fathers and

P laceboijt is equal to one for those fathers with children between the ages of 24–25 from

2008 to 2010.57 From 2010 to 2012, the duration where my analysis ends, P laceboijt is

equal to zero across all states.

The empirical strategy I rely on to detect job-push is conceptually similar to the

one I use for job-lock, demonstrated in equation (4). The main diﬀerence, however, is

that it includes those fathers who did not have EPHI in the previous wave. Therefore,

for the job-push analysis, yijt is equal to one if fathers voluntarily left their jobs without

EPHI or indicated a change in employment status from unemployed to employed in the

current wave. A positive estimate of β1 would provide evidence of job-push, meaning

56My interest is not in examining the placebo eﬀect among those fathers whose youngest child was aged

27–29 because they were not targeted by both the state and federal mandates.

57This is because fathers were not aﬀected by state mandates; however, they would eventually be aﬀected

by the federal mandates.

35

that fathers who did not have EPHI from their employers would be more likely to seek

new jobs with EPHI to cover their child.

I also examine the mandates’ impact on working fathers’ annual earnings or to-

tal monetary compensation by using the fathers who stayed in their jobs with EPHI

during the current wave—a subset of the aforementioned job-lock sample. Since em-

ployers could easily identify the group of working fathers with eligible children, they

might respond to the extra cost of providing dependent coverage by reducing other

types of compensation for this group. To examine whether the cost of the mandate

was transferred to working fathers with eligible children, in equation (4), I replace yijt

with the natural log of the annual earnings and total monetary compensation. I analyze

total monetary compensation because employers might decrease other compensation

(e.g., employer contribution toward deferred compensation) instead of directly adjust-

ing eligible fathers’ earnings to avoid violating non-discrimination laws (Anand, 2017).

I deﬁne this total monetary compensation as the sum of annual earnings and deferred

compensation. Because my outcome variable is not binary in this analysis, I run a lin-

ear regression instead of probit analog of equation (4). If there was any compensation

reduction for those working fathers whose youngest child was eligible for the mandates,

I would expect a negative estimate of β1. An important note in this analysis is that

a small number of responses are automatically omitted when zero compensation was

reported.58

58This omission of responses occurs because I use the natural log of compensation for the dependent variable.
Thus, I omit the fathers who self-reported that they were employed with EPHI in the SIPP—a primary
sample selection criteria for job-lock analysis—but demonstrated zero earnings in the DER. Earnings might
be absent from the DER for some working fathers because their employers failed to report the employees’
wages to the Social Security Administration. These workers without DER data were more likely to work
in private households, construction, agriculture and informal occupations (e.g., street and door-to-door sales
work, dancing or bartending) (Roemer, 2002).

36

2.5 Results

2.5.1 Job-Lock

Table 2.3 shows the evidence for an increase in job-lock among working fathers due to

the dependent coverage mandates. After the mandates took eﬀect, the average proba-

bility of leaving an employer for any voluntary reason was 0.8 percentage points lower

for working fathers with eligible children than for other fathers. This 0.8 percentage

point decrease is a 42 percent decrease in voluntary job separation given that the av-

erage separation rate of ever eligible working fathers before the implementation was

approximately 1.9 percent.59 Column 1 does not include any control variables, and

column 2, the preferred estimate, incorporates all covariates. The last column provides

results with control variables and the state time trends. 60

The magnitude of my results in Table 2.3 is comparable to the eﬀects of sim-

ilar child-targeted mandates on the mobility decisions of working fathers. Barkowski

(2017) ﬁnds that Medicaid eligibility for one household member resulted in a 34 per-

cent increase in the likelihood of a voluntary job separation among working member(s)

in the household. Chatterji et al. (2016) also demonstrate that the ACA prohibition

on pre-existing condition exclusions increased the probability of job separation by 35

percent for married fathers with disabled children compared to fathers with healthy

children.61

59Even when I run a logit regression, I observe similar eﬀect sizes (see Appendix Table 2.10).
60In Tables 2.4, 2.5, 2.6, 2.8 and 2.11, I only report the results with covariates that do not have state time

trends as in column 2 of Table 2.3.

61Chatterji et al. (2016) and Barkowski (2017) focus on whether parents’ reliance on employment for health
insurance decreased; I examine whether it increased. The primary idea, however, remains the same: health
insurance mandates for children could aﬀect fathers’ labor market decisions.

37

Table 2.3: Job-Lock

Voluntary Job Separation

Eligible

Covariates

[1]
-.007†
(.004)

[2]

[3]

-.008*
(.003)
Y

-.009*
(.003)
Y

State Time Trends

Y

N. of Observations [1,000]
Dependent variable means
Ever eligible, before Mandate

11.5

11.5

11.5

.019

.019

.019

In Table 2.4, I examine the robustness of the results. To compare these estimates

with the main results, column 1 is taken directly from column 2 of Table 2.3.62

In

column 2, I expand the control group by including working fathers whose children were

aged 27–33 to see if the result would vary depending on the age range of the children.

In column 3, I also examine whether expanding the time period with the 2001 SIPP

panel would alter the results. Here, I omit ﬁve states (i.e., Wyoming, Vermont, Maine,

South Dakota and North Dakota) because they were sampled together in the 2001

SIPP. As I am unable to verify the exact implementation dates for the mandates in

Georgia, Nevada, South Carolina and Wyoming with more than one source (Goda et

al., 2016, I exclude fathers from these states in column 4. In column 5, I exclude the

state mandates that had student status requirements (i.e., Florida, Idaho, Louisiana,

Massachusetts, North Dakota, Rhode Island and South Dakota).63

In column 6, I

compare the real and the placebo eﬀects, and the resulting estimate of placebo is

62I also repeat the results of Table 2.3 (column 2) in Tables 2.5 and 2.6 for ease of comparison.
63As mentioned in Institutional Details, full-time students aged 19–22 years old before the mandates were
implemented were often considered to be eligible under their parents’ plans. In my main analysis, however, I
assume all working fathers with children aged 19–22 as eligible only after the mandates were implemented.
This may raise a concern whether it is valid to consider the states that required student status as mandated
states because this only applied to students. I therefore examine whether excluding those states would alter
the results signiﬁcantly.

38

−0.003 with 0.009 standard error. This suggests that there was no eﬀect of the state

mandates among those fathers with children who did not meet the state-mandated age

criteria. Still, this column shows that the actual policy change (which resulted in a 0.8

percentage point decrease with 0.004 standard error) is contributing to the main result

as in column 1. In the last column, I exclude 2008 and 2009 responses because fathers

might be aﬀected by the Great Recession, and their labor force decisions during this

time could be diﬀerent compared to those from other periods. For instance, I expect

that voluntary job separation would be signiﬁcantly lower in 2008–2009 because the

overall availability of alternative jobs would be lower. Except for column 7, which has
a −0.011 estimated coeﬃcient, almost all results in this table have a similar magnitude

of around a 0.8 percentage point decrease with statistical signiﬁcance in column 1.64

In Table 2.5, I examine the heterogeneity of the results. Working fathers with

lower education might be less responsive to the mandates because of a lack of under-

standing of the dependent coverage mandates. On the other hand, the working fathers

might be more likely to have children who needed the dependent health coverage be-

cause their children would generally be less educated and less likely to secure jobs with

EPHI. Column 2 shows the eﬀects on working fathers who did not receive a Bachelor’s

degree, and column 3 shows the eﬀects on working fathers who completed a four-year
degree or above. The estimated coeﬃcient on Eligijt is −0.007 with a standard error

0.003 in column 2. This suggests that fathers with less education had less job mobil-

ity as a result of the mandates, supporting the latter hypothesis. Columns 4 and 5

show that fathers whose wives did not have EPHI would be more likely to experience

64Though the result in column 5 is statistically insigniﬁcant, it has a p-value of around 0.13.

39

Table 2.4: Robustness Checks

Voluntary Job Sep.

[1]
Preferred
Table 3 [2]

[2]

[3]

[4]

[5]

[6]

[7]

Eligible

Placebo

-.008*
(.003)

-.007*
(.003)

-.007*
(.003)

-.008*
(.004)

-.006
(.004)

-.011**
(.004)

-.008*
(.004)
-.003
(.009)

Child Aged 19-33

Y

Including 2001 SIPP

Y

w/o States-Unclear Dates

Y

w/o States-Student-Status

Equation (5)

w/o 2008 and 2009

Y

Y

Y

N. of Observations [1,000]

11.5

15.5

14.5

11.0

10.0

11.5

9.6

job-lock because they were the only source of health insurance for the household. The
estimated coeﬃcient in column 4 is −0.009 with a standard error of 0.004, reﬂecting

less job mobility for fathers with wives lacking EPHI after the mandates.

Table 2.5: Heterogeneity Tests

Vol. Job Sep.

[1]
Preferred
Table 2.3 [2]

[2]
Lower Educ. Higher Educ. No Spouse HI Spouse HI

[3]

[4]

[5]

Elig.

-.008*
(.003)

-.007*
(.003)

Obs. [1,000]

11.5

7.80

-.006
(.009)

3.70

-.009*
(.004)

9.20

-.004
(.006)

2.30

Table 2.6 illustrates the results of four falsiﬁcation tests. In column 2, I examine

whether involuntary job separation (e.g., layoﬀ) increased due to the dependent cov-

40

erage mandates. I use the same sample as that in column 1, but I change my outcome

variable from voluntary to involuntary job separation. As involuntary job separation

could not be related to the new eligibility for the mandates, no eﬀect would be expected.

In columns 3 to 5, I investigate whether there were any contemporaneous changes that

aﬀected parents diﬀerently based on the age of their children, which could bias my

results.

In these columns, I consider fathers who were covered by EPHI but whose

coverage was not aﬀected by the mandates (due to the ineligible ages of their chil-

dren) and examine if their behaviors changed when the mandates were implemented.

Therefore, my sample in columns 3-5 comprises working fathers in three groups: those

whose youngest child was between the ages of 8–18, 30–40 and 27–36, respectively. In

column 3, for example, I consider the placebo (state or federal) mandates’ eligibility by

subtracting 11 from the original age eligibility criteria based on fathers whose youngest

child was aged 8–18. If the mandate expanded coverage to dependent children up to

the age of 23, I would consider this state’s placebo age limit to be 12. By doing this,

I can examine whether those working fathers with ineligible children under 19 seemed

to be aﬀected by the mandates. I repeat this process for working fathers with children

aged 30 to 40 in column 4. For these working fathers, I add 11 to the original age eligi-

bility. That being said, if the mandate increased the age limit to 23, I would consider

this state’s placebo age limit to be 34).

One drawback of the two falsiﬁcation tests shown in columns 3 and 4 is that

they do not include any fathers who are in my main sample. To rectify this, I use

the sample containing working fathers whose youngest child aged 27–36 in column 5

of Table 2.6. With this analysis, I can examine whether there were any time-eﬀects.

41

This refers to circumstances that had changed over time and aﬀected parents diﬀer-

ently based on the ages of their children. In this column, I include the same Always

Ineligible fathers whose youngest child was aged 27–29 that I use in my main analysis.

However, I alter the Ever Eligible group—whose children were aged from 19–25—by

adding 11 to the original age limit, resulting in an overall sample of fathers with 27- to

36-year-old children. None of the falsiﬁcation tests have any signiﬁcant eﬀects, and the

point estimates are appreciably diﬀerent from my main ﬁndings in column 1 of Table

2.6.

42

Table 2.6: Falsiﬁcation Tests

[1]
Pref.

[2]
Invol. Sep.

[3]

[4]
Vol. Job Sep.

[5]

Elig. Age-11 Elig. Age+11 Elig. Age+11

Eligible

-.008*
(.003)

-.002
(.003)

.003
(.004)

Observations [1,000]

11.5

11.5

16.5

-.003
(.007)

6.50

for 19-25

.006
(.007)

8.00

2.5.2 Job-Push

Fathers may not only experience job-lock due to these mandates, but also the twin

phenomenon of job-push. In Table 2.7, I examine whether the fathers without EPHI

were incentivized to leave their jobs due to the increase in opportunity costs of staying

in their employment status. Unlike Hamersma and Kim (2009) and Barkowski (2017)

who study the Medicaid expansions, my 1 percentage point estimate of increased vol-

untary job separation of the eligible fathers is not signiﬁcant at a conventional level.

As such, I do not ﬁnd evidence of job-push for these fathers.

One explanation is the time horizon in which parents were aﬀected by the poli-

cies. While Medicaid inﬂuenced parents for a long period of time, the dependent

coverage mandates only aﬀected parents for a shorter period when their children were

in their early 20s. Parents, therefore, might be less motivated to change their employ-

ment status (in this case, ﬁnding a new job with EPHI) for such a short-term beneﬁt.

Additionally, parents who greatly valued insurance for their kids probably would have

moved to such jobs already. Because I only use the sample that consists of fathers

who did not have EPHI through their jobs, this might mean that they had a lower

43

demonstrated need and value of health insurance.

Table 2.7: Job-Push

Voluntary Job Separation

[1]

[2]

[3]

Eligible

Covariates

.012
(.022)

.012
(.020)
Y

.022
(.026)
Y

State Time Trends

Y

N. of Observations [1,000]

2.80

2.80

2.80

2.5.3 Reduction in Compensation

Table 2.8: Annual Earnings and Total Monetary Compensation 1

Eligible

[1]
ln(Earnings)

[2]
ln(Tot. Comp.)

SIPP-DER-BR
-.091†
(.054)

-.079
(.054)

N. of Observations [1,000]

11.0

11.0

[3]
ln(Earnings)
Public SIPP

-.002
(.041)

11.0

To examine whether employers adjusted employee compensation in response to

rising health insurance costs, I analyze the change in total monetary compensation and

annual earnings. Table 2.8 presents the eﬀects of this mandate on earnings and other

compensation for working fathers who did not leave their jobs with EPHI, based on

both the administrative data and the public data. Column 1 presents no evidence for

a reduction in annual earnings while column 2 shows there is weak evidence of decline

in total compensation by about 9 percent.65 This means that employers might try

65The results, however, should be interpreted with caution. As mentioned, non-discrimination laws might
have prevented employers from diﬀerentially compensating employees. In addition, all workers might have

44

to adjust other monetary compensation instead of directly decreasing the earnings for

those fathers with EPHI. Through this examination, I observe that fathers with EPHI

not only experienced job-lock, but also could experience compensation reduction. Said

another way, because the average total compensation of treatment group was about

$70,000 before the implementation of the mandates, a weakly supported 9 percent

decrease in total compensation could result in a $6,300 decrease among fathers with

eligible children after the mandates.66

To compare the results in columns 1-2 with the result based on the public data,

I include column 3 of Table 2.8.67 Unlike the results from the administrative data, I do

not ﬁnd any signiﬁcant eﬀect on compensation by using the public SIPP data alone.68

2.6 Conclusions

While both the state and federal dependent coverage provisions successfully increased

health insurance rates among young adults, previous research did not make it clear

whether the mandates had any eﬀects on their parents. To address this gap, I an-

alyze the eﬀects of both the state and federal mandates on fathers’ dependence on

employment. My investigation is unique in the literature because I bring together

three important analytic features: (1) a focus on fathers (whom are not targeted by

the mandates) whose responsiveness is the key determinant for the eﬀectiveness of the

mandates; (2) a usage of both the state and federal mandates to achieve more credible

borne the cost of the mandate since many non-parents were potential future users of the policy and it would
have been diﬃcult for ﬁrms to implement wage oﬀsets when workers became parents.

66To examine whether including fathers with zero compensation changes my results, I also add one to both
dependent variables for those who had zero compensation and examine the same analysis again in Table 2.11.
This result shows the consistent decrease in compensation, as shown in Table 2.8.

67Although the earnings reported in the public SIPP are monthly, I aggregate them into annual earnings

for each father and use this as an outcome measure for column 3.

68Due to data unavailability, I do not examine the eﬀect of the mandates on total monetary compensation

from the public SIPP data.

45

variation; and (3) a usage of administrative data on the earnings measure that have

not been used in the relevant literature.

I ﬁnd that the mandates decreased voluntary job separation by about 0.8 per-

centage points among eligible working fathers (aged 45–64, with EPHI) than would

otherwise have been. This decrease in voluntary job separation represents that, on

average, 0.8 percentage points of more fathers would stay in their jobs for each wave

than prior to the implementation of the mandates. As such, after one year—comprising

three waves—2.4 percentage points more fathers would remain in their current jobs pro-

viding EPHI.69 If I assume that each father covers one child, my model suggests that

the mandates could increase the young adult dependents who have health insurance

coverage by at least 2.4 percentage points. This approximation of increased coverage

among young adults aligns with another paper that suggests an increase of coverage

among adult dependents about 5.3 percentage points during 2010–2011 (Cantor et.

al., 2012). My estimate, the 2.4 percentage points increase in coverage, is relatively

smaller compared to the 5.3 percentage points and is plausible given that not all fa-

thers considered a job change when they started to cover their newly eligible young

adult dependents. While covering a more broadly deﬁned population, my observa-

tion that the child-targeted mandates could aﬀect parents’ mobility is consistent with

previous ﬁndings (Bansak and Raphael, 2008; Chatterji et al., 2016; Hamersma and

Kim, 2009). Additionally, my estimates are robust to a variety of speciﬁcation checks,

although some eﬀects have a change in magnitude and lose statistical signiﬁcance. I

discover no evidence of job-push, and I ﬁnd weak evidence of compensation reduction

69This conversion between wave and year is necessary for my comparison because I report ﬂow changes for

job mobility, while other papers report change in dependent coverage rates in stocks.

46

among eligible fathers. My paper provides new insights into the eﬀectiveness of the

dependent coverage mandates and emphasizes how health insurance access can have

far-reaching consequences for both targeted individuals and their household members.

Since many other insurance-related changes were implemented in 2014 (e.g., pre-

mium subsidies for private coverage, the Medicaid expansion and individual mandate),

it is important to understand the ways in which the dependent coverage mandates

might be aﬀected. For example, people with incomes below 133 percent of the federal

poverty level (FPL) could qualify for expanded adult Medicaid while those who have

incomes from 133–400 percent of FPL could qualify for premium subsidies for private

insurance. Therefore, these people might have chosen an expanded public coverage

or newly subsidized form of coverage after 2014. My analysis of the dependent cover-

age mandates from 2004 to 2012 implies that these two policies could have decreased

the EPHI-related constraints that both young adults and their parents faced. Addi-

tionally, the repeal of the individual mandate—eﬀective beginning in 2019—could also

contribute to further ﬂuctuation in the rates of dependent coverage and the job mo-

bility of fathers. Due to enforcement of the individual mandate in 2014, young adults’

health insurance take-up could increase, while simultaneously decreasing job mobility

among fathers. The opposite can happen after 2019. With these subsequent changes,

future research might examine how the fathers’ incentives to change jobs could be fur-

ther modiﬁed.

Additionally, as there is a clear trade-oﬀ—an increase in coverage of young adults

and decrease in job mobility among fathers—induced by these mandates, a more thor-

ough welfare analysis is necessary to examine how the mandates aﬀected the economy’s

47

overall well-being and to determine if this policy should be continued.

48

APPENDIX

49

Table B.1: Implementation of the Dependent Coverage Laws

Full Year Implemented Maximum age

Federal Mandate
State Mandates
Colorado
Connecticut
Delaware
Florida*
Idaho*
Illinois
Indiana
Kentucky
Louisiana*
Maine
Maryland
Massachusetts*
Minnesota
Missouri
Montana
New Hampshire
New Mexico
North Dakota*
Rhode Island*
South Dakota*
Utah
Virginia
Washington
West Virginia
Wisconsin

2010

2006
2009
2008
2008
2008
2010
2008
2008
2009
2007
2008
2007
2008
2008
2008
2007
2003
1995
2007
2005
1995
2007
2009
2007
2007

25

24
25
23
24
24
25
23
25
23
24
24
25
24
24
24
25
24
25
24
23
25
24
24
24
26

50

Table B.2: Alternative Regression Results (Logit)

Voluntary Job Separation

Eligible

Covariates

[1]
-.007†
(.004)

[2]

[3]

-.008*
(.004)
Y

-.010*
(.003)
Y

State Time Trends

Y

N. of Observations [1,000]

11.5

11.5

11.5

Table B.3: Annual Earnings and Total Monetary Compensation 2

Eligible

[1]
ln(Earnings+1)
-.225†
(.113)

N. of Observations [1,000]

11.5

[2]
ln(Tot. Comp.+1)

-.239*
(.114)

11.5

Table B.4: Working Mothers’ Job Mobility

Voluntary Job Separation

[1]

[2]

[3]

Eligible

Covariates

.003
(.005)

.004
(.005)
Y

.002
(.005)
Y

State Time Trends

Y

N. of Observations [1,000]

8.80

8.80

8.80

51

Chapter 3. Reconsidering Venti and Wise: Choice or Chance?

3.1 Introduction

Why do many households accumulate substantial wealth by retirement, while many

other households accumulate very little? These are fundamental questions in eco-

nomics, addressed in classic papers from Friedman (1953) to Dynan, Skinner, and

Zeldes (2004), to name just a few. Moreover, this question is of fundamental impor-

tance to numerous policy questions related to optimal taxation, retirement, and the

social safety net.

In companion articles, Venti and Wise (1999, 2001) directly examine the ques-

tion by utilizing data that were superior to that available to previous researchers. In

particular, they made use of the Health and Retirement Survey (HRS), which contained

high-quality data on a wide variety of assets, demographics, health, and previous in-

heritances, as well as near-lifetime earnings from Social Security Administration (SSA)

data. Based on these sets of data, Venti and Wise (2001) write, “Thus we conclude

that the bulk of the dispersion must be attributed to diﬀerences in the amount that

households choose to save.” This central ﬁnding continues to be cited by researchers.70

In this paper, we replicate one of the central analyses presented in Venti and

Wise (2001), but instead use the 2001 Survey of Income and Program Participation

(SIPP). One signiﬁcant beneﬁt of the SIPP over the HRS is that the SIPP provides

lifetime earnings information using Internal Revenue Service (IRS) data, rather than

70For example, relatively recent papers that have cited Venti and Wise (2001) results include Campbell
(2015), Gustman and Steinmeir (2015), Cronqvist and Siegel (2017), De Nardi and Fella (2017), and Lusardi
et al. (2017).

52

SSA data used by Venti and Wise (2001).71 The drawback to SSA earnings measure

is that earnings are only recorded up to the taxable maximum. Importantly, for the

time period analyzed in Venti and Wise (2001), this taxable maximum amount was

low enough that over 30 percent of the HRS sample was at the maximum taxable limit

during their prime earning years, potentially having led to a substantial measurement

error. Such measurement error concerns are potentially problematic because measure-

ment error in one regressor generally biases the results for all regressors in a multiple

regression analysis. Cognizant of this data limitation, Venti and Wise (2001) make use

of lifetime income deciles in their analysis, but it is not possible to assess the extent to

which such a procedure alleviated the data problem.

With our SIPP data, we address this issue directly. We show that there remains

substantial measurement error even when individuals are classiﬁed into deciles: over 30

percent of individuals are misclassiﬁed in each of the top ﬁve deciles of lifetime earn-

ings, and over half of individuals are misclassiﬁed in the 9th decile. We then examine

directly how this misclassiﬁcation aﬀects their main analysis. Our ﬁndings suggest

that the correlation between lifetime earnings and savings was about 50% greater than

what is found when using censored deciles, and almost double the variation of the data

can be explained by lifetime earnings alone.

The rest of the paper is structured as follows. Section 2 brieﬂy summarizes the

insights from a lifecycle model of savings about wealth dispersion. Section 3 discusses

Venti and Wise’s (2001) analysis we replicate. Section 4 provides details of the SIPP

data, and Section 5 presents our replication exercise. We conclude in Section 6.

71While IRS data is now available for the HRS, it was not available at the time of Venti and Wise (2001)
publication. Other papers using the HRS data at the time, such as Haider and Solon (2006), similarly used
the SSA data for lifetime earnings.

53

3.2 Background

The workhorse model for understanding the savings decision is the lifecycle model, in

which households seek to maximize the expected discounted lifetime utility subject to

an asset constraint.72 Such a model delivers the standard prediction that individuals

will save to smooth consumption over time. Thus, this most basic model predicts a

relationship between lifetime earnings and savings at retirement, so that consumption

can be smoothed between the working years and the retirement years.

Even in the basic lifecycle model, households with identical lifetime earnings

may enter retirement with diﬀerent levels of savings. Speciﬁcally, the optimal level of

consumption could increase or decrease over time, depending on whether the subjective

discount factor is less than or greater than the interest rate. Thus, households with

diﬀerent subjective discount factors should choose to save diﬀerently out of lifetime

earnings. In addition, the standard model has been modiﬁed along numerous other

dimensions that could also lead to individuals to choose to save diﬀerentially, including

diﬀerential tastes for retirement, diﬀerential bequest motives, diﬀerential levels of risk

tolerance (leading to diﬀerential choices in savings vehicles), and diﬀerential expecta-

tions about health expenditures, to name just a few. Thus, while the most basic model

predicts a direct relationship between lifetime earnings and savings at retirement so

that consumption can be smoothed, there are numerous reasons why individuals may

choose to accumulate diﬀerent levels of wealth at retirement given the same level of

lifetime income.

72See the discussion in Dynan, Skinner and Zeldes (2004) for a particularly well-targeted discussion of the
lifecycle model and the accompanying literature relevant for our purposes. See Alan et al. (2015) and Bozio
et al. (2017) for a recent contribution that focuses on whether the rich save more. See Benartzi and Thaler
(2007) for a discussion of behavioral factors associated with savings.

54

The link between lifetime income and wealth at retirement would be further

diminished by numerous factors that might broadly be considered as chance. The op-

timal savings rate is determined by one’s expected lifetime resources. Shocks to these

resources, perhaps income shocks related to unexpected spells of unemployment, wealth

shocks related to unexpected inheritances or divorce, or expenditure shocks related to

unexpected medical bills, could all aﬀect retirement wealth.

3.3 Venti and Wise’s Analysis

Venti and Wise (2001) make use of high-quality HRS data to examine the issue of

choice versus chance in a straightforward, direct, and descriptive way. One of their key

analyses is a series of regressions in which they successively regress wealth at retirement

on lifetime earnings and various sets of regressors that are classiﬁed as being related

to chance variables, investment choice variables, and taste variables. Speciﬁcally, the

authors estimate the following household-level regression,

W ealthi = β0 + β(cid:48)

1Lif eEarni + β(cid:48)

2Chancei + β(cid:48)

3Investi + β(cid:48)

4T astei + i

(6)

In their speciﬁcations, Lif eEarni is measured by decile of lifetime earnings in SSA

earnings, which are topcoded at the taxable maximum in each year (we describe the

rest of the regression variables below). The authors explicitly note that they use

deciles of lifetime earnings because of the measurement error induced by using top-

coded annual earnings to calculate the lifetime earnings; in other words, the hope is

that censored earnings data will be suﬃcient to classify individuals into the correct

decile of lifetime earnings.

55

The focus of the regression analysis is not the coeﬃcients per se, but rather the

amount of the variation in wealth that can be explained by these variables. To measure

the amount of the variation that can be explained, Venti and Wise (2001) focus on the

percent reduction of the root mean square error (RMSE), which is the square root of

the variance of the residuals from the regression equation. For comparison, our analysis

will follow suit.

The potential eﬀect of measurement error for linear regression is well-studied

and summarized succinctly in numerous reviews (e.g., Griliches, 1986; Bound, Brown

and Mathiowetz, 2001).

It is useful to begin with the standard results for the case

when just one regressor in a multiple regression suﬀers from classical measurement

error, which is the case when the measurement error is mean-zero and uncorrelated

with the other elements of the model. Namely, the coeﬃcient on the error-ridden

regressor will be downward-biased to an extent that is related to the relative variance

of the measurement error, and the coeﬃcients on the other regressors (assumed to be

measured without error) will be biased with the direction determined by the sign of their

partial correlation with the error-ridden regressor. Speciﬁcally, the other regressors that

have a positive (negative) partial-correlation with the error-ridden regressor will tend

to be upward (downward) biased. See Bound, Brown, and Mathiowetz (2001) for a

precise statement of this result, as well as a discussion for moving beyond this special

case.

These standard results are not directly applicable (6) because lifetime earnings

is not entered linearly, but rather is entered as a collection of decile indicator variables.

With that said, the typically provided intuition goes through for numerous extensions:

56

“using xj as a proxy for x∗
eﬀects of x∗

j will partially, but only partially, control for the confounding

j on the estimates of the eﬀect of other variables on outcomes” (Bound, et al.

2001, p. 3713). In other words, if the censored lifetime earnings deciles inadequately

control for actual lifetime earnings, then the role for lifetime earnings will tend to

be understated and the remaining correlation will spill over to the other regressors

in the regression equation. For example, if education (a “taste variable”) is positively

correlated with lifetime earnings (after controlling for the other variables in the model),

education should be expected to upward biased. In such circumstances, the role for

lifetime earnings would be expected to be understated and the role for education would

be overstated.

3.4 Data

We use wave 3 of the 2001 SIPP. The SIPP is a nationally representative household

survey that collects detailed information on income, wealth, demographics, employ-

ment, and health. The 2001 SIPP can also be linked to the Detailed Earnings Records

(DER) of the IRS. The DER is drawn from the Social Security Administration’s Mas-

ter Earnings File and includes all earnings reported on W-2 tax forms. Unlike the

HRS-SSA dataset, the linked records (SIPP-DER) are not top coded at the maximum

taxable SSA earnings (Bollinger et al., 2015).

While the SIPP is representative of the US population, our purpose here is to

replicate an analysis using the HRS. Thus, we only include SIPP households that satisfy

the primary sample selection criterion of the HRS: Households where the respondent

(or spouse for married individuals) is in the age range of 51 to 61, which we refer to

57

as “HRS-eligible households.” Following the sample construction of Venti and Wise

(2001), we retain households that can be matched to the administrative data, including

those who have zero W-2 earnings for some years.73 Additionally, the household must

have completed a wealth topical module when the survey was conducted.

In Table 3.1, we provide basic descriptives from our analysis sample, as well as

descriptives for all the other HRS eligible households in the SIPP (i.e., those house-

holds not matched to DER earnings histories). As can be observed, the households

in our sample are positively selected in terms of education, income, and wealth. The

amount of selection is greater in these data than what is reported for the HRS sample

that can be matched to SSA earnings histories.74

3.5 Results

Our central research question is the extent to which measurement error in lifetime

earnings due to the use of topcoded Social Security earnings data aﬀected Venti and

Wise’s (2001) conclusions. To estimate the amount of measurement error they faced,

we ﬁrst create a measure of lifetime earnings for our sample that imposes the amount

of censorship faced in the Venti and Wise (2001) sample. To do so, we impose the

same amount of censorship in our data that is reported for the HRS sample used in

Haider and Solon (2006): Venti and Wise’s (2001) do not report censorship, but Haider

and Solon (2006) use the HRS and show censorship. We then classify individuals into

deciles based on 20 years of censored earnings, to mimic the Venti and Wise (2001)

73One diﬀerence between our sample and that of Venti and Wise (2001) is that they additionally exclude
households that reported working for any level of government for ﬁve years. The SIPP does not collect such
information, so we are unable to impose this restriction.

74In Appendix Table 3.5, we provide a direct comparison of the relative selection in the two data sets,

making use of individual results reported in Venti and Wise (2001).

58

Table 3.1: Basic Descriptives for SIPP Household Sample

Matched HRS-Eligible Unmatched HRS-Elig.
Households
(N=2,500)

Households
(N=1,700)

Head Characteristics
Age
Education
Male
Black
Hispanic
Married
Widowed/Divorced/Separated
Poor Health

Spouse Characteristics (if married)
Number of HH with spouses
Age
Education
Male
Black
Hispanic
Poor Health

54.4
14.0
60.0
10.0
1.2
56.0
34.0
12.0

1,400
53.6
13.8
28.0
5.7
0.7
10.7

Household Characteristics
Children
2001 Household Income (public SIPP)
2001 Wealth
Lifetime household earnings-censored
Lifetime household earnings-uncensored

0.24
61,630
498,100
820,700
981,600

55.5
13.5
55.8
11.7
1.2
64.7
32.4
17.6

1,000
53.9
13.5
35.0
7.0
1.0
15.0

0.25
50,310
298,700
.
.

59

variable, and based on 20 years of uncensored earnings.

Table 3.2: Percent of Each Uncensored Classiﬁed into Each Censored

Uncensored Decile
1 (Lowest)
2
3
4
5
6
7
8
9
10 (Highest)

1
99
0
0
0
0
0
0
0
0
0

Censored Decile

2
0
95
3
1
1
0
0
0
0
0

3
0
5
92
3
0
0
0
0
0
0

4
0
0
6
89
4
1
0
0
0
0

5
0
0
0
7
82
8
2
1
0
0

6
0
0
0
0
14
71
8
2
2
2

7
0
0
0
0
0
19
65
10
3
3

8
0
0
0
0
0
0
24
45
16
14

9
0
0
0
0
0
0
0
42
38
21

10
0
0
0
0
0
0
0
0
40
60

Table 3.2 shows the extent to which the censored earnings causes there to be

measurement in lifetime earnings deciles. First, unsurprisingly, there is no measure-

ment error in the lowest decile: All individuals who were classiﬁed into the ﬁrst decile

indeed belonged in the ﬁrst decile. Perhaps surprisingly, measurement error creeps into

the measure even by the 2nd decile: 95 percent of individuals who should have been

classiﬁed into the 2nd decile were classiﬁed as such based on the censored earnings

data, with 4 percent incorrectly classiﬁed into the 3rd decile. The correct classiﬁcation

rate then becomes successively worse: 80 to 90 percent were correctly classiﬁed in the

4th through 5th deciles, 71 percent in the 6th decile, 65 percent in the 7th decile, 45

percent in the 8th decile, 38 percent in the 9th decile, and then back to 60 percent for

the 10th decile. Thus, for two of deciles with the highest income, less than half of the

households are classiﬁed correctly.

60

Table 3.3: Comparing the Venti and Wise to Our SIPP Varibles

Lifetime

Venti and Wise using the HRS
20 years of topcoded-
SSA earnings earnings deciles

Our SIPP Analysis
20 years of W-2 earnings

Wealth variables Bequeathable wealth

: 15 categories,
imputations based on
bracket info

Bequeathable wealth
: 14 categories,
imputations based on
longitudinal info

Deﬁned beneﬁt pensions
: included

Deﬁned beneﬁt pensions
: not available

Taste variables

Education: coding not required

Education: 5 categories

Race/Ethnicity: info not provided

Race/Ethnicity: 4 categories

Chance variables Marital status: 4 categories

Marital status: 3 categories

Children: indicator for any;
number of children

Children: indicator for any;
number of children

Health: poor self-reported
health for head (and spouse)

Health: poor self-reported
health for head (and spouse)

Age: continuous for head

Age: continuous for head

Inheritances: indicator for any;
amount <1980, 1980-1988, and >1988

Inheritances: not available

Choice variables

Percent held in
10 wealth categories

Percent held in
8 wealth categories

61

To assess the extent to which this measurement error in lifetime earnings aﬀects

their key analysis, we repeat the regression in equation (6) while attempting to follow

the Venti and Wise (2001) speciﬁcation as closely as possible. However, the SIPP

does not ask the same questions as the HRS, so we are not able to replicate Venti

and Wise’s (2001) analysis exactly. To highlight the similarities and diﬀerences in our

speciﬁcations, we compare them directly in Table 3.3. The main diﬀerence between

Venti and Wise (2001) and our analysis is that we do not include information on deﬁned

beneﬁt pension wealth or on inheritances.

Table 3.4: Reduction in RMSE

Lifetime earn
Lifetime earn + Chance
Lifetime earn + Invest
Lifetime earn + Chance + Invest
Lifetime earn + Chance + Invest +Taste

Censored Uncensored 4th

VW (2001) Deciles
5.1
9.1
13.0
15.3
16.0

11.9
13.3
22.6
24.5
27.7

Deciles
17.2
18.4
26.3
29.2
31.3

Poly.
20.4
24.1
26.9
32.6
34.8

We present our key results in Table 3.4, in which we assess how well the regres-

sors of equation (6) predict retirement wealth based on the reduction of the RMSE.

Column (1) repeats the results reported in Venti and Wise (2001). Column (2) repli-

cates their analysis with the 2001 SIPP, censoring lifetime earnings as it is in Venti

and Wise (2001). While the reductions in RMSE are markedly higher across all sets of

regressors, the pattern of adding regressors is largely the same: The inclusion of chance

variables, investment variables, and taste variables all increase the reduction in RMSE.

With that said, it is interesting that the reductions in RMSE are noticeably larger in

the 2001 SIPP for all regressor sets. Perhaps this diﬀerence is due to our exclusion of

62

deﬁned beneﬁt pension wealth, but given that deﬁned beneﬁt pension wealth is usually

a function of earnings and years of service, we doubt this is the case.75

The purpose of our analysis is to assess the extent to which measurement error

in lifetime earnings aﬀected the analysis, which can be assessed by comparing column

(2) to columns (3) and (4). Our preferred estimates are in column (4). The role of

lifetime income in predicting retirement wealth goes up substantially. When comparing

columns (2) and (4), the raw diﬀerence in the role of lifetime earnings almost doubles,

from 11.8 percent reduction in RMSE with censored deciles to 20.5 with lifetime earn-

ings included as a polynomial. Thus, our results suggest that the potential role for

lifetime earnings is dramatically understated in Venti and Wise (2001).

Second, as discussed in Section 2, measurement error in one variable will gener-

ally bias the results for all other variables. This can be observed in the smaller increase

in the total reduction in RMSE for the full model when comparing columns (2) and

(4)—the reduction in RMSE when all variables are included increased only from 27.9 to

34.6. This is consistent with the view that, by only “partially controlling” for the role

of lifetime earnings due to the censored nature of the data, the remaining variables in

the regression are also biased. Thus, the role of lifetime earnings did not just increase,

but the importance of other variables declined. In column (2), the amount of reduction

in RMSE that is observed by just including lifetime earnings is about 42 percent of the

overall reduction (comparing the 11.8 percent reduction to the 27.9 overall reduction).

In column (4), the same role of lifetime earnings is 60 percent of the overall reduction

(comparing the 20.5 reduction to the 34.2 overall reduction).

75In other words, given that deﬁned beneﬁt pension wealth is often strongly related to the same factors
that determine lifetime earnings, we would have expected that the inclusion of deﬁned beneﬁt pension wealth
would have delivered even larger reductions in RMSE.

63

3.6 Conclusion

In this paper, we replicate an inﬂuential analysis by Venti and Wise (1999, 2001) that

seeks to understand the determinants of retirement wealth. Despite the better data

available in the HRS along numerous dimensions, their analysis still faced an important

data problem: the measure of lifetime earnings was subject to fairly serious topcoding

concerns. We use W-2 data in the 2001 SIPP to assess the extent to which the topcoding

in the HRS aﬀected the results. Our ﬁndings indicate that association of lifetime

earnings, measured both by its absolute importance and by its relative importance in

reducing the RMSE, with retirement wealth is much greater than suggested by their

analysis. While much variation remains in the accumulation of retirement wealth, our

results suggest that the simple and direct role that lifetime earnings plays should not

be overlooked.

While the ﬁndings in this study are instructive, further work remains. First, we

provide results for the 2001 SIPP panel. Similar analyses should be undertaken with

the 1996, 2004, and 2008 panels. Second, we closely follow Venti and Wise’s analysis

strategy because of the potential role of measurement error. With that said, another

inﬂuential paper on savings behavior, Dynan, Skinner and Zeldes (2004), uses panel

data on wealth. Their paper could also be replicated with SIPP panels, thus providing

a comprehensive examination of savings behavior with one data set.

64

APPENDIX

65

Our main research question is to determine the extent to which measurement error

in lifetime earnings deciles inﬂuenced the conclusions in Venti and Wise (1999, 2001).

Thus, we attempt to impose the same degree of measurement error in the SIPP data.

To do so, we rely on the censorship rate reported in Haider and Solon (2006), who use

the same HRS Social Security earnings histories, because Venti and Wise (1999, 2001)

do not report the censorship rate in their sample.

In Table 3.6, we report the taxable limit for the 20 years before the 1992 HRS

and the censorship rate reported in Table 3.1 in Haider and Solon (2006). In Haider

and Solon (2006), the sample is composed of only male respondents who were 59-61.

For our primary analysis, we take the 59-61 men in the 2001 SIPP and ﬁnd the level

of earnings that would provide the same rate of censorship. We report this earning

level in column (3) of Table 3.6. We then use this earnings value as the topcode for all

individuals in our 2001 SIPP analysis sample (men and women, regardless of age).

To assess the sensitivity of our results to this procedure, we also compute the

top-coded earnings value that we would ﬁnd if we used all men ages 51-61. We report

this alternative topcode value in column (4) of Table 3.6. As can be observed, the

top-code values are quite similar. We also replicate Table 3.2 in the text based on

these alternative top-code values, showing the results in Table 3.7. Again, we ﬁnd the

degree of measurement is quite similar. Finally, we repeated the key analysis in Table

3.4 based on censored earnings deciles (column 2), delivering estimates of 11.8, 12.5,

22.6, 24.8, and 27.8. None of the estimates vary by more than 0.3 as compared to the

values reported in Table 3.4.

Our key dependent variable is bequeathable wealth, which we obtain from the

66

SIPP 2001 wave 3 topical module. Table 3.8 provides detailed information about the

wealth measures we use. We divide the variables into nine asset categories that broadly

correspond to those categories used by Venti and Wise (2001). The main diﬀerence

between our wealth variable and the Venti and Wise (2001) wealth variable is that we

do not include information on deﬁned beneﬁt pensions.

Table C.1: Comparing Administrative Data Availability

HH in survey year
Percent female
Age
Percent non-white
Education
Percent married

SIPP-

HRS-

HRS-

SIPP-
matched unmatched matched unmatched
56,610
50.0
55.5
13.4
13.6
69.2

52,430
53.3
55.6
16.7
13.2
70.0

54,253
53.0
55.6
15
12
76

53,434
54.0
55.4
13
12
76

67

Table C.2: Determining Censorship in SIPP

Censorship Rate Equivalent Top-

SSA Maximum
Taxable Earnings Reported in
Haider and
Solon (2006)
9.1
10.4
12.2
13.6
12.7
13.4
14.3
15.1
14.7
17.2
18.8
22.5
26.7
40.0
36.3
37.1
37.1
39.5
49.6
55.3

Years Before Relevant to
Survey
1
2
3
4
5
6
7
8
9
10
11
12
13
14
15
16
17
18
19
20

1992 HRS
53,400
51,300
48,000
45,000
43,800
42,000
39,600
37,800
35,700
32,400
29,700
25,900
22,900
17,700
16,500
15,300
14,100
13,200
10,800
9,000

Equivalent Top-
Code for 2001

Code for 2001
SIPP Using 59-61 SIPP Using 51-61
Men
73,190
68,930
67,270
56,350
58,100
57,440
57,410
52,190
50,260
46,830
44,430
40,920
37,880
28,000
29,380
27,030
26,710
24,380
19,640
16,960

Men
79,900
72,830
68,760
61,340
61,760
60,100
56,380
53,270
52,280
47,480
44,780
40,920
36,590
28,140
29,040
27,300
25,550
23,350
17,900
15,900

Table C.3: Men 51-61 Topcode Values

Uncensored Decile
1 (Lowest)
2
3
4
5
6
7
8
9
10 (Highest)

1
100
0
0
0
0
0
0
0
0
0

2
0
94
4
1
1
0
0
0
0
0

Censored Decile

4
0
0
6
88
4
1
0
0
0
0

5
0
0
0
8
82
7
2
1
0
0

6
0
0
0
0
13
72
8
2
2
2

7
0
0
0
1
0
19
65
10
3
3

8
0
0
0
0
0
0
24
46
17
12

9
0
0
0
0
0
0
0
41
39
20

10
0
0
0
0
0
0
0
0
39
61

3
0
6
91
3
0
0
0
0
0
0

68

Table C.4: 2001 SIPP Wealth Variables

Category
Business

Elements
Value of ﬁrst business (tvbva1)
Total debt of ﬁrst business (tvbde1)
Value of second business (tvbva2)
Total debt of second business (tvbde2)

Checking/Savings

Amount in interest earning account (tiaita)
Amount in non-interest checking account (talicha)

Bonds/U.S. Securities Amount of bonds/securities (timia)

Face value of U.S. savings bonds (talsbv)

Stocks

Value of stocks/funds (esmiv)
Amount of debt on the stocks/mutual funds (esmimav)

Real estate – house

Current value of residence (tpropval)
Principal owed on mortgage (tmip)
Market value of mobile home (tmhval)
Debt of mobile home (tmhpr)

Real estate – other

Market value of rental property (trtmv)
Principal owed on rental property (trtpri)
Equity in other real estate (tothreva)

Vehicles

Retirement

Debt

Market value of three vehicles (tcarval1, tcarval2, tcarval3)
Amount owed for ﬁrst, second and third vehicles
(ta1amt, ta2amt, ta3amt)

Market value of IRA (talrb)
Market value of Keogh (talkb)
Market value of 401k (taltb)
Current face value of life insurance (talliv)

Amount owed for store bills/credit cards (ealidab)
Amount of loans owed through credit union or bank (ealidal)
Amount of other debt (ealidao)

69

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