WORKING PAPER SERIES

The Effect of Job Loss on Bank Account Ownership

Ryan M. Goodstein

Federal Deposit Insurance Corporation

Mark J. Kutzbach

Federal Deposit Insurance Corporation

September 2022

Forthcoming in Journal of Money, Credit & Banking

FDIC CFR WP 2022-13

fdic.gov/cfr

The Center for Financial Research (CFR) Working Paper Series allows CFR staff and their coauthors to circulate 

preliminary research findings to stimulate discussion and critical comment. Views and opinions expressed in CFR Working 

Papers reflect those of the authors and do not necessarily reflect those of the FDIC or the United States. Comments and 

suggestions are welcome and should be directed to the authors. References should cite this research as a “FDIC CFR 

Working Paper” and should note that findings and conclusions in working papers may be preliminary and subject to 

revision.
The Effect of Job Loss on Bank Account Ownership*

Ryan M. Goodstein†

Mark J. Kutzbach‡

September 2022 

ABSTRACT: We estimate the effect of job loss on households’ bank account ownership using a 

novel assembly of data: FDIC-sponsored biennial supplements to the Current Population Survey 

(CPS), linked to respondents’ work history in surrounding months constructed from the basic 

monthly CPS. We leverage differences in the timing of unemployment spells across respondents 

to plausibly identify the effect of job loss. Our estimates indicate the effects of job loss are quite 

large in magnitude. For example, households that experienced a job loss in the months leading up 

to the FDIC survey are about 18 percentage points more likely to be unbanked than households 

that lost a job in the subsequent year. This effect is roughly three-quarters of the sample mean 

unbanked rate among the lower-income, renter households that we study. Job loss also leads to 

increased use of other transaction products and services that might substitute for a bank account, 

including prepaid cards, check cashing, and money orders. 

                                                            

*

 Views and opinions expressed in this paper reflect those of the authors and do not necessarily reflect those of the 

FDIC or the United States. We thank Manju Puri for discussions of early stages of this research. We thank Rosalind 

Bennett, Kenneth Brevoort, Karyen Chu, Scott Fulford, Yosh Halberstam, and Julieta Yung for helpful comments, 

as well as participants at the Society of Government Economists (Virtual Seminar: Unbanked Households, Poverty, 

and Taxation), the FDIC Center for Financial Research seminar series, and the 2022 Boulder Summer Conference 

on Consumer Financial Decision Making. 

†

 Senior Economist, Center for Financial Research, Division of Insurance and Research, Federal Deposit Insurance 

Corporation, Washington, DC. Email: rgoodstein@fdic.gov. 

‡

 Senior Financial Economist, Center for Financial Research, Division of Insurance and Research, Federal Deposit 

Insurance Corporation, Washington, DC. Email: mkutzbach@fdic.gov. 
1

1. INTRODUCTION 

For most households in the United States, bank accounts are a fundamental tool for handling 

household finances. Accounts at federally insured depository institutions are covered by deposit 

insurance and other consumer protections, providing consumers with a safe place to keep and 

build savings. Bank accounts can help consumers save time and money when conducting 

financial transactions (Barr 2012; Armstrong 2016), and having a relationship with a depository 

institution facilitates access to credit products that can be used to smooth consumption in the 

event of income or expense shocks (Brevoort and Kambara 2017; FDIC 2018). 

Recognizing the potential benefits of account ownership, expanding households’ 

participation in the banking system has long been a focus of public policy.1 Coincident with 

these efforts, the proportion of U.S. households without an account at an insured depository 

institution has been declining over the past few decades, as illustrated in Figure 1. Still, as of 

2019 about 5.4 percent of (or 7.1 million) U.S. households were “unbanked”, meaning that no 

one in the household had a checking or savings account at a bank or credit union (FDIC 2020). 

To inform the ongoing efforts of policymakers and other stakeholders, it is important to 

understand the barriers that contribute to households’ not having an account. 

This paper focuses on the role of job loss. Shocks to employment are likely to have an 

important effect on bank account ownership for several reasons. First, many households in the 

U.S. have little liquid savings and do not have an adequate financial cushion to cover income or 

expense shocks. Median net worth among the bottom quartile of U.S. families in 2019 was about 

$300 (Bhutta et al. 2020), and nearly 4 in 10 households in 2019 indicated that if faced with a 

$400 emergency expense, they would cover it using something other than cash or its equivalent 

(FRB 2019). In the event of a job loss, such households may find it difficult to manage their cash 

flows to avoid bank account fees or falling below minimum balance requirements.2

 Job loss 

                                                            

1

 For example, the U.S. Treasury’s Office of Consumer Policy has undertaken several initiatives to increase lowand moderate-income households’ access to financial services and financial education dating back to (at least) 2008. 

The FDIC chartered an Advisory Committee on Economic Inclusion in November 2006; the committee periodically 

convenes to provide the FDIC with advice and recommendations on important initiatives focused on expanding 

access to banking services by underserved populations. More recently, the FDIC has embarked on a #GetBanked 

public awareness campaign to encourage unbanked households to open insured accounts, for example working with 

Treasury and the IRS to encourage households to open a bank account to facilitate receipt of Economic Impact 

Payments following the COVID-19 pandemic. (See, e.g., https://www.irs.gov/newsroom/how-to-get-an-economicimpact-payment-if-you-dont-have-a-bank-account.) 2

 Not all bank accounts have such fee structures. According to a survey by MoneyRates.com “More than 37% of 

checking accounts now have no monthly maintenance fees.” Richard Barrington, October 5, 2021. 
2

compounds this issue because it might result in a household losing direct deposit of a paycheck, 

which might have qualified the household for a waiver from such fees or balance requirements. 

Understanding how economic factors, such as job loss, affect household bank account 

ownership is particularly timely given the COVID-19-related economic recession and uneven 

economic recovery. Figure 1 shows that while there has been a secular decline in the unbanked 

rate among U.S. households, during recessionary periods this decline has slowed or reversed. 

We analyze data from biennial FDIC-sponsored supplements to the Current Population 

Survey (CPS), linked to the basic monthly CPS. In a novel use of these data, we take advantage 

of the sample rotation structure of the CPS to construct a short panel with information on 

households’ work history in the months leading up to and after the month the FDIC survey is 

administered. We limit our analysis to lower-income, renter households to focus on those with 

low wealth who are more likely on the margin of bank account ownership. Such households 

made up 19.4 percent of all households and 67.9 percent of unbanked households in the U.S. in 

2019. The unbanked rate among lower-income, renter households in 2019 was 18.8 percent, 

compared to 2.1 percent among other households.3

 

The key empirical challenge for this analysis is the potential endogeneity of job loss with 

respect to bank account ownership. While previous literature establishes that unbanked rates are 

higher among unemployed populations conditional on demographic and socioeconomic controls, 

the cross-sectional nature of such analyses makes it difficult to rule out the possibility that 

unobserved factors correlated with job loss might also affect a household’s likelihood of bank 

account ownership.4 For example, households with lower educational attainment or financial 

literacy may select into jobs with a higher turnover rate, and may also be less inclined to open 

and maintain a bank account. 

                                                            

https://www.moneyrates.com/research-center/bank-fees/. The Cities for Financial Empowerment Fund’s 2021-22 

Bank On National Account Standards include a minimum balance requirement of no more than $25 and monthly 

maintenance fees of $5 or less. 

3

 These reported unbanked rates and shares of households are weighted estimates using data from the 2019 FDIC 

survey. As detailed below, we define lower-income, renter households as those with less than $40,000 in annual 

income and that do not own their place of residence. The complement includes households that earn at least $40,000 

in annual income or are homeowners (or both). 

4

 A notable exception is Rhine and Greene (2013), who use the U.S. Census Bureau’s Survey of Income and 

Program Participation (SIPP) to examine transitions out of banking using longitudinal data and finds financial 

shocks to be a factor. However, that analysis does not consider any confounding factors that may affect both job loss 

and unbanked status. See Section 2 for a discussion of the relevant literature. 
3

To overcome this identification issue, we leverage differences across households in their job 

loss status or timing of job loss. In our main empirical analyses, we compare bank account 

ownership status for a treatment group compared to two alternative control groups. The treatment 

group (“Job Loss”) consists of households in which at least one adult loses a job in the months 

leading up to the FDIC survey. The first control group (“Remain Employed”) includes 

households in which no adults lose their job in the months leading up to the FDIC survey. The 

second control group (“Subsequent Job Loss”) includes households that lose their job in the year 

subsequent to the FDIC survey. 

The latter control sample, in particular, advances the empirical literature on this topic by 

focusing on a set of households that are likely similar to the treated households in terms of 

unobserved characteristics and that experience an analogous economic shock, just at a later date. 

However, we acknowledge that in practice there are differences in certain observable 

characteristics of the treatment and control groups (e.g., by race/ethnicity), which may cast doubt 

on our identification assumption. We address this concern in detail below, in part by showing 

that under reasonable assumptions the potential scope of omitted variable bias is minimal. A 

second limitation with our empirical approach is that the sample size of the Subsequent Job Loss 

control group is quite small, reducing the precision of our estimates and hindering our ability to 

explore heterogeneity in effects. Therefore, we present results using both control samples 

throughout the paper. 

Our results indicate that job loss has an economically and statistically significant effect on 

bank account ownership across a variety of specifications and subsamples. In our preferred 

specification, we find that households experiencing job loss are 12.5 and 17.7 percentage points 

more likely to be unbanked than households in the Remain Employed and Subsequent Job Loss 

control samples, respectively. These differences are large relative to the sample mean unbanked 

rates of 15.8 and 24.1 percent, respectively. We find that the job loss effect is transitory among 

households that are re-employed (i.e., the adult that experienced a job loss finds employment 

within a year), but the effect is persistent among households that remain unemployed. Pointing 

toward a pecuniary mechanism, we find that effects of job loss are most pronounced among the 

lowest income households we analyze, and that job-losing households are especially likely to 

report being unbanked for reasons relating to finances. We also find evidence that job loss leads 
4

to increased use of prepaid cards, money orders, check cashing, and pawn shop loans (though not 

payday loans, which typically require a bank account as well as income). 

The remainder of this paper is organized as follows. Section 2 provides background including 

a review of the relevant literature; Section 3 describes the data and empirical specification; 

Section 4 presents the estimation results; and Section 5 provides concluding thoughts including 

potential policy implications.

2. BACKGROUND 

Accounts at federally insured depositories (i.e., banks or credit unions) offer several potential 

benefits to consumers. They provide a safe place to store and build savings, offering deposit 

insurance and consumer protections such as upfront disclosures about fees and rates, provisions 

for financial privacy, and protections against error and fraud. Bank accounts can save consumers 

time and money when conducting financial transactions such as receiving income, paying bills, 

and purchasing goods and services.5

 Bank accounts also facilitate access to credit for “credit 

invisible” consumers (those that lack credit history at one of the three nationwide credit reporting 

agencies), as lenders may underwrite credit products using deposit account balances and 

transaction history (Brevoort and Kambara 2017; FDIC 2018).6

Despite these potential benefits, bank account ownership differs substantially across 

segments of the U.S. population. For example, unbanked rates are higher among lower-income 

households, renter households, less-educated households, Black and Hispanic households, 

working-age disabled households, and households with income volatility, as shown in Appendix 

Figure A1. Such cross-sectional differences in unbanked rates have persisted for at least the past 

few decades and might be attributable to a variety of factors, which we summarize here. 

Households with low liquid savings or more volatile income may find traditional bank 

accounts difficult to manage due to minimum balance requirements, restrictions on access to 

                                                            

5

 By some estimates (e.g., Barr 2004; Armstrong 2016), the costs of conducting financial transactions without a bank 

account may be in the hundreds of dollars per year. 6

 Some lenders are leveraging technology to underwrite credit products using bank account information. For 

example, Petal-branded credit cards (issued by WebBank) are underwritten using cash-flow data from bank 

statements. Home mortgage lenders may also use technology to underwrite using bank account information. For 

example, as of September 2021 Fannie Mae’s Desktop Underwriter now allows lenders to, “...automatically identify 

recurring rent payments in the applicant’s bank statement data to deliver a more inclusive credit assessment.” 

(Fannie Mae press release, “Fannie Mae Introduces New Underwriting Innovation to Help More Renters Become 

Homeowners” August 11, 2021.) 
5

funds, or potential fees including those for insufficient funds or overdrafts (e.g., Hogarth et al. 

2004; Hogarth et al. 2005; Barr 2004).7 Households that have had past difficulties in managing 

accounts may not be able to qualify for a new bank account (e.g., Campbell et al. 2012). Further, 

geographic proximity to financial institutions may also play a role. Caskey (1994) argues that a 

relative scarcity of bank branches in lower-income and minority neighborhoods may inhibit these 

households’ ability to open and maintain an account.8 Finally, households of different 

backgrounds have different tastes and preferences which affect their demand for having bank 

accounts. For example, some households may lack trust in financial institutions, may lack 

familiarity with banks, or may avoid accounts due to limited financial literacy or numeracy.9

Knowing the relative importance of such factors is key for informing policy interventions to 

encourage households to obtain bank accounts. 

This paper focuses on the role of employment. In particular, to the extent that households that 

suffer an unexpected or involuntary job loss have lower and more volatile household income, 

they may have more difficulty managing their cash flows and keeping enough money in the 

account to avoid fees or falling below minimum balance requirements. In short, for some lowsavings households experiencing an income shock, the cost of maintaining certain bank accounts 

may outweigh the value added of those accounts. 

While previous empirical evidence on the role of employment is somewhat limited, 

subjective data suggest that financial considerations are likely critical.10 For example, among 

unbanked households in 2019, nearly half did not have an account because they, “Don’t have 

enough money to meet minimum balance requirements,” and for over one-in-three, “Bank 

                                                            

7

 Recognizing that minimum balance requirements and other account fees might make bank accounts unattractive or 

difficult to manage for households with lower or more volatile income (FDIC 2016), policymakers and other 

stakeholders have developed a template for depository accounts that might be well-suited for such households. For 

example, see the FDIC’s Model Safe Accounts Pilot (FDIC 2012) and the Cities for Financial Empowerment Fund’s 

Bank On National Account Standards for 2021-2022 (CFE 2020). 

8

 Goodstein and Rhine (2017) show that households residing in neighborhoods with limited access to bank branches 

(e.g., no branches within 5 miles) are less likely to have a bank account and more likely to use nonbank transaction 

services, although effects are modest in size. In related work looking at the mortgage market, Ergungor (2010) finds 

that originations increase and interest spreads decline when there is a bank branch located in a low- to moderateincome neighborhood. 

9

 See Hogarth et al. (2004) for a survey of the early literature on these points. More recent evidence includes 

Northwood and Rhine (2017), who show that patterns of bank account ownership and use of nonbank financial 

services differ among immigrant households (and relative to native-born households), for example by whether they 

reside in an ethnic enclave or by the level of maturity of their home country’s retail banking system. 

10 Qualitative interviews elicit a variety of rationales for closing a bank account when money is tight, as in the case 

of job loss. For example, some households opt to use money orders, rather than checks, to avoid nonsufficient funds 

fees and to make sure that certain bills are paid even if others are not (KCFED 2010 p. 6; Servon 2017 p. 7 and 17). 
6

account fees are too high,” or, “Bank account fees are too unpredictable.” However, nonfinancial reasons are also frequently cited; over one-in-three unbanked households in 2019 didn’t 

have an account because they, “Don’t Trust Banks,” or, “Avoiding a Bank Gives More 

Privacy.”11 A limitation of these data is that comparable information is not observed for banked 

households, which makes it difficult to assess the extent to which such factors contribute to 

households’ likelihood of maintaining a bank account. 

The FDIC’s 2013 survey included a series of subjective questions designed to uncover causal 

linkages between life events and households’ transitions into and out of the banking system. The 

results suggest that unemployment is quite important; among households that became unbanked 

within the previous year, about 45 percent had experienced a job loss or significant income loss 

over the same period, and 34 percent indicated that the job loss or significant income loss 

directly contributed to the household becoming unbanked (FDIC 2014). 

Rhine and Greene (2013) find that banked households that suffer a loss of income or 

employment are likely to become unbanked, based an analysis of Survey of Income and Program 

Participation (SIPP) longitudinal data between 2004 and 2006. But this study suffers from the 

potential limitation that changes in employment status may be correlated with unobservable 

differences across households. 

The main innovation of this paper is that we leverage differences in the timing of job loss 

across households to more cleanly identify the effect of job loss on the likelihood of being 

unbanked. We describe our identification strategy in detail in the next section. Further, relative to 

the prior literature, our analysis covers a longer and more recent period (years 2011 to 2019) that 

encompasses substantial developments in the provision of banking services. For example, over 

the past decade the number of physical bank branches in the U.S. has declined, use of online and 

mobile banking services has become more widespread, as has the availability of alternatives to 

bank accounts such as prepaid cards and online transaction accounts like PayPal and Venmo. In 

light of these developments, we explore whether the effects of job loss on account ownership has 

changed over time. 

                                                            

11 Estimates described in this paragraph are from FDIC (2020); results from earlier FDIC surveys are qualitatively 

similar. 
7

3. METHODOLOGY 

3.1. Data

The CPS is a monthly survey of the U.S. civilian noninstitutional population, representative 

at the national- and state-level. In addition to serving as the primary source of information on the 

labor force characteristics of the U.S. population, the CPS also collects data on demographic 

characteristics, and on supplemental information that varies each month. 

One such supplement to the CPS is the FDIC-sponsored Survey of Household Use of 

Banking and Financial Services, first administered in January 2009 and then biennially in June 

between 2011 and 2019.12 We use the 2011 to 2019 FDIC surveys in this study, pooling the data 

across survey years. The key outcome variable of interest for this analysis is whether a household 

is “unbanked”, meaning no one in the household had a checking or savings account at the time 

the FDIC survey was administered. 

We also examine households’ use of other financial transaction services that might substitute 

for (or complement) the transaction services provided by a bank account, including prepaid 

cards, nonbank money orders, and nonbank check cashing services. Finally, we study 

households’ use of two nonbank credit products: pawn shop loans and payday loans. Such 

products are disproportionately used among households that may not have access to 

“mainstream” credit products such as credit cards or unsecured personal loans.13 These nonbank 

transaction and credit products lack the consumer protections of a bank account and mainstream 

credit, and may result in higher costs to the consumer. 

We use household identifiers to link the FDIC surveys to the Basic Monthly CPS, which 

includes household data as well as data for each person in the household. Specifically, our 

analyses include controls for demographic characteristics (age; sex; race and ethnicity; nativity; 

marital status; educational attainment) and income and employment characteristics (annual 

household income; self-employment; full-time status; industry; number of adults and employed 

                                                            

12 Prior to 2019, the FDIC-sponsored supplement to the CPS was known as the Unbanked/Underbanked supplement. 

Because some of the outcomes we study are not available or measured differently in the January 2009 supplement, 

we exclude these data from our analysis. 

13 Unless noted otherwise, the outcomes we examine are observed in the FDIC survey in each of the supplement 

years between 2011 and 2019. In some years the FDIC survey also collects information about use of other nonbank 

financial transaction services and credit products, including bill payment services and rent-to-own services. 
8

adults in household).14 For simplicity we use the attributes of the “householder” (i.e., the person 

(or one of the people) who owns or rents the home) for demographic characteristics, and we use 

information from the household’s first month-in-sample (MIS) in the Basic Monthly CPS to 

describe its employment characteristics. If the householder is not employed in the first month, we 

obtain employment characteristics from the first employed person in the household. (See 

Appendix Table A1 for a detailed list of the control variables and how they are constructed.)

Finally, we use the time series of the Basic Monthly CPS to construct a short panel with 

information on households’ work history in the months leading up to and after the FDIC survey 

month.15 To do so, we take advantage of the CPS sample rotation structure, illustrated in Figure 

2. 

Sampled households are in the CPS for 4 consecutive months, are then out for 8 months, and 

then return for another 4 consecutive months. Thus, each FDIC survey is administered in June to 

a sample that can be disaggregated into one of eight “rotation groups”, based on the household’s 

MIS in that survey month. Work histories begin for the second rotation group in May, the third 

rotation group in April, and the fourth rotation group in March. 

To focus our analysis on changes in labor force status that are most likely to impact 

household finances and least likely to be voluntary, we limit our sample to persons aged 20 to 59 

in their first month of observation (MIS=1) in the CPS. We require that persons do not attrite in 

the first four months-in-sample, to ensure consistency of the households in our sample.16 We also 

require that each household has at least one person employed in the first month of observation. 

Finally, we focus our analysis on a subset of households that are likely to be on the margin of 

bank account ownership due to financial constraints. Specifically, we limit the sample to renter 

(i.e., non-homeowner) households with annual income below $40,000. Such households made up 

19.4 percent of all households and 67.9 percent of unbanked households in the U.S. in 2019 

(FDIC 2020). Renter households and those in the lowest income quintile have very little wealth 

or savings, so loss of income might almost immediately affect such households’ ability to meet 

                                                            

14 As a robustness check we also included controls for geography (e.g., Census region; metropolitan status); doing so 

had little effect on our estimates.   15 To link across months, we use the household fields specified above as well as the CPSIDP field curated by CPSIPUMS that tracks individuals across months (Flood et al. 2018). 

16 The attrition requirement is not very restrictive; 85.5 percent of persons and 90.2 percent of householders meeting 

the other sample requirements respond to each of the first four months in sample. The pattern of our main results is 

also robust to imposing more stringent restrictions on attrition. However, this comes at a cost of reduced sample 

size, and sample restrictions based on attrition may not be innocuous if attrition is non-random. 
9

minimum balance requirements and absorb fees associated with overdrafts and negative 

balances.17 

3.2. Empirical Specification 

We estimate linear probability models of the form 

PሾUnbanked௜௧௥ሿ ൌ α ൅ job_loss௜β൅X௜

ᇱ

γ൅Y௜

ᇱ

δ ൅ μ௧ ൅ π௥ ൅ ε௜௧௥ (1) 

where i is an index for households, and t and r are indices for the FDIC survey year and CPS 

rotation group, respectively.18 

The dependent variable Unbanked௜௧௥ is a binary indicator equal to 1 if the household is 

unbanked, and equal to 0 otherwise. The key explanatory variable is job_loss௜, a binary indicator 

equal to 1 if the household experienced a job loss in the months leading up to and including the 

month of the FDIC survey, and equal to 0 otherwise. (Below we describe precisely how the job 

loss indicator is defined.) The unbanked rate among households that did not experience a job loss 

leading up to the FDIC survey serves as the counterfactual – or the expected outcome absent 

treatment. We interpret our estimate for the parameter β as the effect of job loss on the likelihood 

of being unbanked. A positive coefficient would be consistent with job loss inducing households 

to become unbanked. 

X௜ is a vector of household-level demographic characteristics, which may reflect 

households’ tastes and preferences or correlated supply-side factors (e.g., geographic proximity 

to bank branches). Y௜ is a vector of the household’s income and employment characteristics in 

the first month the household is observed. μ௧ is a vector of survey year fixed effects, and π௥ is a 

vector of CPS rotation group fixed effects. These controls account for potential time trends and 

for seasonality of households starting the CPS in different months and also control for 

                                                            

17 The SIPP reports median value of assets by household characteristics (Median Value of Assets for Households, by 

Type of Asset Owned and Selected Characteristics: 2019). Renter households have $4,084 in net worth (compared 

to $305,000 for owners), with only $2,200 in a financial institution (compared to $11,700 for owners). Households 

in the lowest quintile of annual income (approximately equal to our cutoff) have $6,030 in net worth and only $650 

in a financial institution (U.S. Census Bureau 2020). 

18 We use linear probability models for ease of interpretation, particularly in subsequent specifications that include 

interaction terms. We estimate the regression models using Stata 16, with the robust option for estimating standard 

errors (StataCorp 2019). The magnitude of effects implied by our main results is similar to estimates using probit 

models, as described below. 
10

differences in month-in-sample for when a household responds to the FDIC survey. ε௜௧௥ is an 

error term. 

The key empirical challenge for this study is the potential endogeneity of job loss with 

respect to bank account ownership. Despite the extensive set of control variables in the model, it 

is difficult to rule out the possibility that the error term ε௜௧௥ is correlated with unobserved factors 

that also affect households’ likelihood of having a bank account. One concern is that a financial 

shock resulting in a negative account balance could lead to terminating a bank account and 

directly affect work. For example, a financial shock that prevents a worker from repairing a 

broken vehicle could contribute to job loss. Another potential concern is that households with 

unobserved, lower financial literacy or less trust in financial institutions might be less likely to 

maintain a bank account and might tend to select into jobs with a higher turnover rate. In either 

case (as well as others not described here), controlling for observable differences may not be 

sufficient. 

To address this identification issue, we leverage differences across households in their job 

loss status or timing of job loss. Specifically, we take the following approach. First, we limit the 

sample to households in rotation groups 2, 3, or 4 in the month the FDIC survey is administered 

(i.e., they are in their 2nd, 3rd, or 4th MIS in the June CPS). For this subset of households, we 

observe labor force status in the months leading up to (and including) the FDIC survey, as well 

as in the subsequent year. We then compare the probability of bank account ownership between a 

treatment group and two alternative control groups, as illustrated in Figure 3. 

The treatment group (Job Loss) consists of households in which at least one adult employed 

in the first month of observation (MIS=1) becomes unemployed in their second month of 

observation (MIS=2).19 Depending on the specific rotation group, the job loss may occur in 

April, May, or June. Limiting our analysis of job loss to the recently unemployed focuses the 

analysis on a group experiencing a recent change in financial circumstances and with comparable 

prospects for re-employment, as job finding rates decline with duration of nonemployment.20

                                                            

19 We consider all job types in our definition of employment, including wage and salary workers and the selfemployed. In our empirical model, we include controls for self-employment status, full time (vs. part time) status, 

and a categorical variable for industry type. See Table 1 for details. 20 We identify job loss using contemporaneous responses to construct a work history, as opposed to using 

retrospective responses on duration of unemployment. Duration responses may differ from contemporaneous 

responses as respondents may report the duration of search even if that search period included short-term jobs while 

searching. Kudlyak and Lange (2018) find that work histories explain job finding rates more completely than job 

search duration alone. Another concern with retrospective responses is recall bias, as is discussed by Evans and 
11

The first control group (Remain Employed) consists of households in which no adults 

employed in the first month of observation (MIS=1) lose a job up through the fourth month of 

observation (MIS=4). Note that we cannot rule out an involuntary job change following a very 

brief period of unemployment. Most unemployment spells last less than two months, but from 

the CPS, it is not possible to measure spells lasting less than a month. 

The second control group (Subsequent Job Loss) consists of households that have at least one 

adult employed in the fifth month of observation (MIS=5) who then suffers a job loss in the sixth 

month of observation (MIS=6). With this construction, the job losses in the second control group 

occur exactly one year later than job losses in the treatment group. These households must also 

have at least one person employed in the first month of observation, though that person need not 

be the one that ultimately loses a job. 

Households that do not meet the above criteria for the treatment or control groups are 

dropped from the analysis sample. We estimate the regression models separately for: the Job 

Loss treatment group vs the Remain Employed control group (specification A), and the Job Loss 

treatment group vs the Subsequent Job Loss control group (specification B).21

Our identification assumption is that, conditional on the other control variables in the model, 

the job loss experienced by the treatment group is exogenous with respect to the households’ 

decision over bank account ownership. In specification A, which parallels the approach in Rhine 

and Greene (2013), this assumption is somewhat tenuous as discussed above. It may be the case 

that households that suffer a job loss may be unobservably different than households that remain 

employed. Even so, we make several significant sample restrictions and include a rich set of 

controls to mitigate these concerns. 

The identification assumption in specification B is not as susceptible to those concerns. 

Households in both the treatment and control groups are observed to suffer a job loss during the 

period of observation; the only difference is in the timing of the unemployment spell. These 

groups are therefore likely to be similar along unobserved dimensions, mitigating potential 

endogeneity concerns. However, one drawback of this second approach is that in practice the 

                                                            

Leighton (1995), with regards to the Displaced Worker Supplement to the CPS. For results with alternative 

definitions of job loss, see the Appendix. 

21 In addition to the empirical specifications described here, we explored using a variety of other intuitively similar 

specifications, and found that the estimation results were qualitatively similar. We use the specifications presented in 

the paper because of their (relative) simplicity and because they are less restrictive in terms of sample size. 
12

sample size of the Subsequent Job Loss control group is quite small, reducing the statistical 

precision of our estimates and limiting our ability to explore heterogeneity in effects. To 

facilitate comparisons with previous literature and to gauge the degree of selection that may be 

present in the first Remain Employed model, we present regression results from both 

specifications. 

4. RESULTS 

4.1. Descriptive Statistics 

Table 1 presents unweighted sample means for the 179 households in our treatment sample 

(Job Loss) and for the control samples (A. Remain Employed and B. Subsequent Job Loss) with 

5,409 and 103 households, respectively.22 The unbanked rate for the treatment sample (32.4 

percent) is substantially greater than the two controls (15.3 percent and 9.7 percent respectively). 

Use of other financial products and services such as prepaid cards and nonbank money orders is 

also higher among the treatment group compared to the control groups. 

Table 1 also shows that observable characteristics of the treatment and control groups differ 

along certain dimensions. In Appendix Table A2, we regress job loss, our explanatory variable of 

interest, on the other controls. The estimates from those regressions show, in a multivariate 

context, which observable characteristic factors are most closely associated with treatment. In 

both regressions, the treatment households are more likely to be Black (non-Hispanic) and less 

likely to be full time employed. Relative to the remain-employed control group, treated 

householders are also more likely to be Hispanic and less likely to be in the higher portion of the 

household income distribution (20,000 - 39,999). Relative to the Subsequent Job Loss control 

group, treated householders are less likely to be married and more likely to work in the retail and 

service sectors. The treated group is also substantially less likely than the Subsequent Job Loss 

control group to be observed in survey year 2019.23 

That certain observable characteristics of the Job Loss treatment group differ from the 

Subsequent Job Loss control group is surprising, and may cast some doubt on our argument that 

                                                            

22 Attrition of persons and households contributes to the smaller sample size of the subsequent job loss sample 

relative to the treatment sample. See Section 4.3 for further discussion. 

23 The Subsequent Job Loss control group disproportionately consists of observations from survey year 2019 

because, for this year, the subsequent year spans April to June 2020, when COVID-19 related job losses were 

widespread. See Section 4.4 for further discussion on this point. 
13

these groups are likely to be similar along unobserved dimensions. We address this concern in 

detail in Section 4.4 below. 

4.2. Main Estimation Results 

Table 2 presents OLS estimates of the effect of job loss on the probability of being unbanked. 

Each column presents estimates from a different regression. In panel A the control is the Remain 

Employed group. The estimate in the first column indicates that when controlling only for survey 

year and rotation group fixed-effects, households that lost a job are 16.9 percentage points (pp) 

more likely to be unbanked relative to households without a job loss. Adding controls for 

demographics, income, and employment characteristics to the model (column 2), the estimated 

effect falls to 12.5pp, statistically different from zero at the 5% level. 

Panel B presents the results from our preferred specification, where the control is the 

Subsequent Job Loss group. The estimate in the third column indicates that households that had a 

job loss in the months preceding the FDIC survey were 18.7pp more likely to be unbanked than 

households that had a job loss in the year following the survey. Adding the full set of controls to 

the specification (column 4) has little effect; the point estimate falls to 17.7pp. 

These estimates indicate that among the lower income, renter households we study, the effect 

of job loss on household bank account ownership is quite large in magnitude and similar across 

specifications. The point estimate in column 2 is about 79% of the overall unbanked rate for the 

Remain Employed analysis sample, and about 73% of the overall unbanked rate for the 

Subsequent Job Loss analysis sample. Although not directly comparable, our estimates suggest 

that the effect of job loss is somewhat larger in magnitude than the estimates from Rhine and 

Greene (2013).24

Further, the estimated effects of job loss are quite large compared to the other control 

variables in the model, shown in Appendix Table A3. For example, the point estimates on job 

                                                            

24 Reconciling our results with Rhine and Greene (2013) is not straightforward because of differences in the 

empirical specifications and samples being analyzed. Rhine and Greene (2013) specify a model with separate 

controls for job loss, income loss, and health insurance loss; in practice a job loss could result in a household losing 

income and/or health insurance. Under the assumption that the effects are additively separable, their estimates imply 

that the total effect of a job loss, loss of income of 50% or more, and loss of health insurance on likelihood of 

transitioning into unbanked status is about 50% of the mean rate of transition in their sample. This point estimate is 

smaller than the roughly 75% effect we estimate. Some of this difference may be due the samples being analyzed. 

Rhine and Greene (2013) estimate their model using all households in the SIPP (between 2004 and 2006), while we 

limit our analysis to lower-income renter households for whom effects are likely larger. 
14

loss are of similar magnitude to the effects associated with being Black or Hispanic and are 

larger than the effects associated with educational attainment (i.e., having an Associate’s degree 

or higher), household income (i.e., income of $20-40k relative to $20k or less), and nearly all of 

the other control variables in the model. 

As discussed in the methodology section, the identification assumption for the analysis using 

the Remain Employed control group may be tenuous due to omitted variable concerns. However, 

the fact that the economic magnitudes of the effects in columns (2) and (4) are similar, especially 

when compared to their respective sample means, suggests that these identification concerns may 

not be much of an issue in practice.25 It is also worth noting that for the Subsequent Job Loss 

analysis, adding controls for household demographics, income, and employment characteristics 

has little impact on the point estimate of the job loss effect specifications (comparing columns 3 

and 4). This suggests that the scope of any omitted variable bias may be relatively small, to the 

extent that selection on observables is informative about selection on unobservables.26

We now explore heterogeneity in the effects of job loss with respect to family income, 

race/ethnicity, and survey year; estimates are presented in Table 3. Panel A (columns 1 and 2) of 

Table 3 shows results for the analysis where the control group is Remain Employed, and panel B 

(columns 3 and 4) shows results for the Subsequent Job Loss control group. We caution that 

because of the relatively small sample size used in the latter analyses, the estimated effects are 

statistically imprecise and in some cases may be counterintuitive. (The estimates in Table 3 are 

also presented graphically in Appendix Figures A2, A3, and A4.) 

Panel (i) of Table 3 presents regression results from a specification where the job loss 

indicator is interacted with an indicator for household income between $20-40k. Perhaps 

unsurprisingly, the estimated job loss effect differs sharply by household income. Among 

households with less than $20,000 in household income (the omitted category of the interacted 

variable), job loss increases the likelihood of being unbanked by 20.3pp and 29.8 pp in columns 

(2) and (4), respectively. In both cases these effects are more than 100% of the sample mean 

unbanked rate. The effects of job loss are substantially smaller among households with $20-40k 

                                                            

25 An alternative interpretation is that impact of potential omitted variable bias does not appear to be larger for the 

Remain Employed analysis than for the Subsequent Job Loss analysis. 26 We return to this point in Section 4.4, where we implement the methods of Oster (2019) to show that the scope of 

omitted variable bias is likely small. 
15

in income. For example, the estimates in column four indicate that for this group, job loss leads 

to a roughly (0.298 – 0.226=) 7.2 pp increase in the likelihood of being unbanked.27

In contrast, the estimates in panel (ii), column (2) indicate that the effects of job loss do not 

systematically differ by race and ethnicity. The point estimates on the Hispanic and Other Race 

interaction terms are negative and is very close to zero for the interaction on Black households; 

none of these estimates are statistically different from zero at the 10% level. The same is true in 

column (4) with the exception of the interaction term on Black households; this estimate is large 

and statistically significant. Overall the evidence is mixed, but our reading of these results is that, 

conditional on the other controls in the model, the effect of job loss on probability of being 

unbanked is broad-based across race and ethnicity. 

Panel (iii) of Table 3 explores whether the effect of job loss on being unbanked varies over 

the years of our analysis sample. As discussed earlier, our analysis spans a period of time that 

saw substantial evolution in the landscape for financial transaction products and services, 

including the advent of mobile banking, declining availability of bank branches, and increasing 

availability of other transaction products including prepaid cards and online payment accounts 

such as PayPal and Venmo. However, the estimates in columns 2 and 4 suggest that job loss 

effects are generally quite stable across survey years. This holds true even for the Subsequent Job 

Loss control group in survey year 2019, among whom the job loss occurred during the COVID19 pandemic.28 

An important question for policy is whether households that become unbanked because of a 

job loss remain unbanked for a long duration, or whether the effect is more transitory. We cannot 

directly examine the duration of households’ “unbanked spells” following a job loss, because we 

                                                            

27 As a check on the breadth of our results, we re-estimated the analysis using a broader population of households. 

For this broader analysis (not shown), we define a Remain Employed and a Subsequent Job Loss sample without the 

restriction to lower-income renters (those households who are not homeowners and who have income below 

$40,000 in the last year). Applying the regression model to each of those samples, we find that, overall, households 

with a job loss are more likely to be unbanked. However, when we include an indicator for lower-income renter 

households and interact it with job loss, we find that the effect of job loss is substantially larger for lower-income 

renter households than for the complement of households (about three times larger in the broader Remain Employed 

sample and about six times larger for the broader Subsequent Job Loss sample). We acknowledge that effects of job 

loss on bank account ownership may be more widespread than the lower-income renter population we focus on here, 

but we believe that we can make the strongest case for causal interpretation among this subset of households. 

28 For the subsequent job loss control group sample in 2019, the job loss would have occurred in April, May, or June 

2020. Because job losses were so widespread during the COVID-19 pandemic, one might be concerned about 

differences in selection (e.g., less negative selection) into job loss for this group. However, the estimates in panel 

(iii) of Table 3 suggest this is not much of an issue in practice. Further, in Section 4.4 we show that results are 

similar if we drop survey year 2019 from the sample. 
16

only observe a household’s bank account ownership status in the month the FDIC survey is 

administered. 

We take a different approach, examining whether bank account ownership as observed in the 

FDIC survey is affected by the incidence of job loss roughly one year prior. Appendix Figure A5 

provides an illustration of the identification strategy used for this “Persistence” specification. 

The sample consists of households that are in rotation groups 5 through 8 at the time of the FDIC 

survey. Among these households, we define a “Job Loss Previous Year” treatment group that 

includes households with an adult that was employed in their first month of observation (MIS=1) 

and then unemployed in the second month of observation (MIS=2). The control group “Remain 

Employed Previous Year” consists of households where all adults who were employed in their 

first month of observation remained employed through the fourth month of observation (MIS=4). 

Households that do not meet either criteria are dropped from the analysis.29 

Estimation results from this analysis are presented in Table 4. In the specification with full 

controls (column 2), a job loss in the previous year increases the likelihood of being unbanked by 

5.9 percentage points, statistically significant at the 10 percent level. The magnitude of this effect 

is about 41% of the sample mean unbanked rate, somewhat smaller than the magnitude of the 

more contemporaneous job loss effects presented in Table 2 (a 12.5pp effect, at 79 percent of the 

respective sample mean). 

Columns 3 and 4 of Table 4 present estimated effects when we disaggregate the treatment 

(Job Loss Previous Year) into two mutually exclusive groups based on the labor force status of 

the job loser in the first month observed in the survey year (i.e., MIS=5). About one-in-three 

treatment households are in the “Not Re-employed” group; around two-in-three treatment 

households are in the “Re-employed” group. Strikingly, the entire effect of job loss in the 

previous year is driven by the subset of households for whom the unemployment spell was 

relatively longer-duration, as proxied by the Not Re-employed group. Among households for 

whom the job loss was a shorter-duration event (as proxied by the Re-employed group), the 

likelihood of being unbanked was similar in magnitude to (and not statistically different from) 

the control group. 

                                                            

29 We examined several alternative specifications to the Persistence specification presented here; results (not shown 

for brevity) were qualitatively similar. We also note that the Persistence specification described here is analogous to 

the main analysis using the Remain Employed control group, and acknowledge that the specification is subject to 

similar identification concerns. 
17

We next explore whether households that suffer a job loss are more likely to use certain 

financial products and services that may substitute for the transaction services that a bank 

account provides. Each column and panel of Table 5 presents estimation results from a separate 

empirical specification similar to equation 1 (for the Remain Employed and Subsequent Job Loss 

control groups in panels A and B), except that the dependent variables listed as column labels 

indicate the use of a financial product or service.30 The estimates in the first three columns of 

Table 5 indicate that job loss leads to increased use of prepaid cards (in Panel A), nonbank 

money orders, and nonbank check cashing services, respectively. Together with our earlier 

finding that job loss reduces the likelihood of bank account ownership, these results suggest that 

households may turn to such products to handle their financial transactions needs following a job 

loss.31 

In the fourth and fifth columns of Table 5 we examine whether job loss increases the 

likelihood of using certain nonbank credit products, specifically pawn shop loans and payday 

loans.32 Column 4 of Table 5 indicates that job loss leads to a higher likelihood of taking out a 

pawn shop loan, although the estimate is not statistically significant in panel B, where the control 

group is Subsequent Job Loss. In contrast, the effect of job loss on use of payday loans is a 

precisely estimated zero in both specifications. This null finding is consistent with our main 

result that job loss increases the probability of being unbanked, given that having a bank account 

and having income is generally a prerequisite for taking out a payday loan. These results suggest 

that households experiencing job loss may both become unbanked and turn to credit products 

that do not require a bank account.33 

 

                                                            

30 We note that for each of the outcome variables examined in Table 5, the FDIC supplement questionnaire asks 

whether the household used the product within 12 months of the FDIC supplement month (June). Thus there is a 

potential timing issue, in that the outcome measure may reflect use in months prior to when the treatment (job loss) 

actually occurred. For the estimates to be interpreted as reflecting the causal effect of job loss, we must assume that 

variation in use of the product in the months prior to the treatment is uncorrelated with the incidence of job loss, 

conditional on the other controls in the model. 

31 In unreported results, we find that job loss makes households more likely to be both unbanked and to use nonbank 

money orders as well as to be both unbanked and use nonbank check cashing services (we find mixed results for 

being unbanked and using a prepaid card). 

32 Households may use such credit products to smooth consumption after adverse shocks (see, e.g., Dobridge 2018). 

33 In unreported results, we find that job loss makes households more likely to be both unbanked and to use a 

pawnshop loan. We do not find that job loss is associated with an increased likelihood of being unbanked and using 

a payday loan. Nicolini and Cude (2019) find that households with lower financial well-being (in terms of feeling 

secure in their financial future), and especially unbanked households, were more likely to use a pawn shop. 
18

4.3. Results from Supplemental Analyses 

We now provide results from supplemental analyses which show that our estimated job loss 

effects are generally consistent with the pecuniary mechanism by which we expect job loss to 

affect bank account ownership. Specifically, we examine how job loss effects differ by whether a 

household reports a “financial” vs. “non-financial” reason for being unbanked, and whether, at 

person-level, effects are larger for the individual losing the job compared to others in the 

household. We also attempt to shed light on dynamics by exploring whether job loss effects 

differ by households’ recency of becoming unbanked, and how effects differ by the month-tomonth timing of job loss relative to the FDIC survey. 

Table 6, panels (i) and (ii) show how job loss effects differ depending on whether the 

household cites “financial” or “non-financial” reasons for being unbanked, respectively.34 If the 

effects we estimate are attributable to job loss (and not some correlated unobserved factor), we’d 

expect the magnitude of the effects to be larger for financial reasons compared to non-financial 

reasons. Consistent with this intuition, the estimates in columns (1) and (2) of panel (i) show that 

effects of job loss on likelihood of being unbanked for financial reasons are large in magnitude. 

However, the estimated effects of job loss on being unbanked for non-financial reasons are a bit 

mixed. For the Remain Employed specification the estimated effect of job loss on being 

unbanked for non-financial reasons is small and statistically insignificant, as shown in column 1 

of panel (ii). But for the Subsequent Job Loss specification in column 2, the point estimate for 

the effect of job loss on being unbanked for non-financial reasons is about the same size as the 

estimate in panel (i), where being unbanked for financial reasons was the outcome. 

Next we explore whether job loss effects differ by the composition of individuals within a 

household. First, we allow effects to differ for households with one working adult compared to 

households with two or more working adults. It seems plausible that job loss effects for the latter 

group might be smaller, to the extent that for these households the financial impact of a job loss 

may be less pronounced relative to total household income. The estimates in Table 7 offer some 

                                                            

34 Specifically, in panel (i) the dependent variable is an indicator equal to 1 if the household is unbanked and cites 

any of the following as the main reason for being unbanked: “Previously had an account but the bank closed it”, 

“ID, credit, or banking history problems”, “Do not have enough money”, “Bank account fees or minimum balance 

requirements are too high” (in 2011); “ID, credit, or banking history problems”, “Do not have enough money to 

keep in account or meet minimum balance”, “Account fees too high or unpredictable” (in 2013); “ID, credit, or 

former bank account problems”, “Do not have enough money to keep in account”, “Account fees too high”, 

“Account fees unpredictable” (in 2015, 2017, and 2019). All other reasons for being unbanked including 

nonresponse are explained in panel (ii). 
19

support for this hypothesis. For example, looking at results for the Remain Employed control 

group in column 1, panels (i) and (ii), the point estimate is slightly bigger for households with 

one employed adult (13.8 pp) compared to households with two or more employed adults (9.3 

pp). But these estimates are not statistically different from each other, and relative to the mean 

unbanked rates for these samples, the magnitudes of the effects are similar. 

To this point, we’ve analyzed outcomes measured at the household level, including bank 

account ownership and use of other financial products and services. We do so because, to the 

extent that adults in a household may share a bank account (or their use of other financial 

products and services) to handle household finances, household-level bank account ownership is 

arguably the most relevant measure for informing public policy.35 

However, understanding how job loss affects bank account ownership at person-level is also 

of interest. This is particularly true to the extent that job loss affects the affordability of a bank 

account. For example, without direct deposit of a paycheck, fees associated with a minimum 

balance requirement may no longer be waived.36 

Table 8 presents person-level estimates of job loss on the probability of being unbanked. 

First, to facilitate comparison with the estimates in Table 7, in panels (i) and (ii) we split the 

sample into persons residing in households with one employed adult or two or more employed 

adults, respectively. While the point estimates of the person-level effects of job loss on bank 

account ownership are generally larger than the household-level estimates presented in Table 7, 

they are of similar magnitudes when expressed as a percentage of the sample mean unbanked 

rates. 

Panel (iii) of Table 8 shows how job loss effects on person-level unbanked rates differ 

depending on who in the household suffers a job loss. Ex-ante, we expect that a person’s 

likelihood of having a bank account should be more affected by that person suffering a job loss 

compared to a job loss suffered by another adult in the household.37 Our results are consistent 

                                                            

35 Further, as a practical matter, most of the information collected in the FDIC supplements to the CPS is at 

household-level. The exception to this is bank account ownership, which is collected both at household- and personlevel for years 2011 through 2019. 

36 “One of the easiest ways to circumvent checking account fees is to have your paycheck, pension or Social 

Security benefit electronically deposited into your account. Many banks require a minimum monthly amount in 

“qualifying” direct deposits from an employer, corporation, government entity or retirement benefits administrator 

to waive monthly account fees.” Libby Wells, ‘8 ways to avoid monthly checking fees’, Bankrate.com, Sept. 20, 

2021. 

37 It’s also plausible that “own” and “other” job loss effects would be similar in magnitude, to the extent that 

resources are shared within households, and if bank account fee structures (e.g. minimum balance requirements, 
20

with this hypothesis. For example, the estimates in column 1 indicate that an “own” job loss 

increases the likelihood of a person being unbanked by 18.6 pp, compared to 11.5 pp for “other” 

job loss. 

The last analyses presented in this section examine the dynamics of the job loss effect. Doing 

so is a challenge because of data limitations. While we observe work history in the months 

leading up and subsequent to the FDIC survey, we only observe unbanked status in the month 

the FDIC survey is administered. Instead, we take advantage of households’ self-reported 

duration of being unbanked and differences in households' timing of job loss relative to the FDIC 

survey to shed light on how quickly job loss may lead to households' becoming unbanked. 

Columns 1 and 2 of Table 9 present estimation results from alternative specifications in 

which the dependent variable conditions on whether the household is “recently” or is “longerterm” unbanked, respectively. Specifically, a household is categorized as recently unbanked if it 

became unbanked within 12 months of the FDIC survey, and as longer-term unbanked if it 

became unbanked more than 12 months prior (or never had an account).38 

The specification in panel (i) is analogous to our main Remain Employed control group 

specification (from Table 2, panel A).39 For this specification, because the job loss “treatment” 

occurs within a few months of the FDIC survey, we expect the job loss effects to be concentrated 

in the recently unbanked group, and the effects on being longer-term unbanked to be zero. 

Consistent with this intuition, the estimate in column 1 indicates job loss has a statistically 

significant effect on the likelihood of being recently unbanked, and the magnitude is quite large -

- the point estimate is 256% of the sample mean value. However, the estimate in column 2 is 

counter-intuitive, indicating that job loss has a positive and statistically significant effect on 

likelihood of being longer-term unbanked. While the magnitude of the estimated effect in 

column 2 is smaller than the corresponding estimate in column 1 when expressed relative to the 

sample means, this result is nonetheless puzzling. One possible explanation is that job loss might 

                                                            

waivers for direct deposit) do not have a meaningful impact on bank account ownership in practice. However, a 

finding that “other” job loss effects are larger than “own” job loss effects would be counter-intuitive. 38 We code households with unknown duration of being unbanked as a zero; results are robust to dropping such 

households. Results are also similar if we drop from the analysis all households that report they never had a bank 

account. About two-thirds of longer-term unbanked households report they never had a bank account. 39 Results from the main Subsequent Job Loss specification are qualitatively similar to the Remain Employed results 

in panel (i). We don’t include these results in Table 9 both for brevity and because we cannot employ a comparable 

identification strategy for the “persistence” specification in panel (ii). 
21

inhibit transitions of longer-term unbanked households into the banking system; some of these 

households might have opened a new account had they not suffered an employment shock.40 

Table 9, panel (ii) presents results using the Persistence specification (analogous to Table 4). 

In this case the job loss “treatment” occurs at least a year prior to the month of the FDIC survey, 

so the job loss effects should be concentrated in the longer-term unbanked group. As expected, 

the estimate in column 2 indicates that a job loss in the previous year increases the likelihood of 

being longer-term unbanked by 5.3 pp, significant at the 10 percent level. In contrast, the 

estimated effect on being recently unbanked in column 1 is a precisely estimated zero. 

Finally, we examine how effects vary across households based on the timing of their job loss 

relative to the FDIC survey. As illustrated in Figure 3 the Job Loss treatment group suffers the 

job loss either two, one, or zero months prior to the FDIC survey, depending on whether they are 

in rotation group 4, 3, or 2 respectively. To the extent that households proactively close their 

accounts soon after suffering a job loss then we might expect the effect to occur nearly 

contemporaneously with the incidence of job loss, and the magnitudes of effects to be similar 

across rotation groups. Alternatively, if households don’t close their accounts until after drawing 

down their accounts and potentially being charged fees for falling below minimum balance 

requirements or overdrafts (or if banks are involuntary closing accounts for these reasons) then 

there may be some delay before account closure. In this case we’d expect effects to be largest for 

rotation group 4 (job loss in April) and decreasing in subsequent rotation groups. 

Figure 4 plots estimates of the job loss effect by rotation group, for the Remain Employed 

and Subsequent Job Loss control groups in panels A and B, respectively. The figures are 

generated from OLS estimates of specifications that include a full interaction of the indicator for 

job loss with the categorical variable for rotation group. To provide another point of comparison 

in the figure, we add to the sample households in rotation group 1 who otherwise meet the 

sample requirements.41 For rotation group 1 households in the Job Loss treatment group, the job 

                                                            

40 FDIC (2018) estimates that about 3.9 percent of U.S. households were “recently banked” in 2017, meaning they 

had an account at the time of the FDIC survey but did not at some point in the 12 months prior. 

41 Specifically, we apply all the sample filters used for the main analysis sample, including the requirement that at 

least one adult is employed in the first month-in-sample (which for rotation group 1 is the month of the FDIC 

survey). 
22

loss occurs in the month following the FDIC survey; if job losses are largely unexpected, we the 

job loss effect should be close to zero for these households.42 

Consistent with this intuition, Figure 4 shows that the point estimates of the job loss effect 

are close to zero for households in rotation group 1 for both the Remain Employed and 

Subsequent Job Loss control groups. We find larger point estimates in line with our main 

estimates for each of the rotation groups 2 through 4, without a clear time trend. While some of 

these rotation group estimates are statistically significant from zero, they are not (alone or in 

combination) statistically different from the “effect” for rotation group 1. While the point 

estimates are fairly similar across rotation groups 2 through 4 which suggests the effects occur 

fairly soon after job loss, the imprecision of the estimates inhibits drawing any strong 

conclusions. 

 

4.4. Identification and potential omitted variable bias 

As discussed above, Table 2 and Appendix Table A2 show that our Job Loss treatment group 

differs from our preferred Subsequent Job Loss control group along certain observable 

dimensions, including race/ethnicity, marital status, and FDIC survey year. These differences are 

surprising given the similarities in how the treatment and control groups are constructed. 

One potential explanation is uneven attrition of households from the control sample. As 

detailed in the Data section, when selecting our analysis sample we filter out households with 

any persons that attrite in the first four months-in-sample (MIS), but don’t filter out households 

based on subsequent attrition. Because attrition is potentially non-random, differences in 

observable characteristics could arise because our Job Loss treatment group includes some 

households that attrite after the fourth month-in-sample (MIS), while by construction households 

in the Subsequent Job Loss control group must remain in sample through at least the sixth MIS.43 

To assess the potential impact of such attrition on our results, we re-estimate the model on a 

“No Attrition” sample where we filter out households with any adults that attrite in any of the 

eight MIS. However, as shown in panel A of Appendix Table A4, differences in observable 

characteristics across treatment and control groups of the No Attrition sample are similar to those 

                                                            

42 Alternatively, if job losses are anticipated by some households, we might see positive effects of job loss on 

unbanked status in the month of the FDIC survey, even though the job loss occurs subsequently to the FDIC survey. 

43 Rivera Drew, Flood, and Warren (2014) discuss patterns in attrition across monthly waves of the CPS, noting that 

attrition is especially prevalent between the fourth and fifth MIS. 
23

from our main analysis sample (Table 1), suggesting that these differences aren’t driven by 

attrition. In any case, estimating equation (1) on the No Attrition sample results in job loss 

effects on unbanked status (Table 10, panel (i)) that are qualitatively similar to our main results 

(Table 2).44

Another potential explanation for observable differences between our treatment and 

Subsequent Job Loss control group samples is that, for observations from survey year 2019, the 

control group’s job losses occurred in April, May, or June 2020, during the COVID-19 

pandemic. If the COVID-19 recession affected a broader, less “negatively selected” set of 

households, including these households in the control group may introduce upward bias in our 

estimated effects of job loss for the treatment sample. To assess this concern, we dropped year 

2019 observations from our sample and re-estimated the model. Panel B of Appendix Table A4 

shows that dropping year 2019 observations does not substantially reduce observable differences 

between the treatment and control groups.45 And as shown in panel (ii) of Table 10, estimated 

job loss effects are quite similar to our main results in Table 2, mitigating selection concerns 

associated with the COVID-19 recession. 

A third possible explanation for the differences in observable characteristics between the Job 

Loss treatment and Subsequent Job Loss control samples is selection related to the duration in 

months before the first observed job loss. Recall that to establish a set of households with similar 

characteristics at the start of our longitudinal analysis (e.g., income earning households), all 

households in our sample have at least one employed adult in the first month-in-sample. Thus, 

treatment households suffer a job loss in the second month while the Subsequent Job Loss 

control households have a job loss in month six. If duration until job loss is related to 

unobservable characteristics (e.g., “chronic” job losers) that also affect demand for banking 

services, our estimates for the Subsequent Job Loss analysis may be biased. However, as shown 

in Table 10 panel (iii), our results are robust to removing the sample selection requirement that at 

least one adult is employed in the first MIS, thereby removing the difference in duration to 

unemployment between the treatment and control samples. Further, very few households in our 

                                                            

44 That our estimates are not very sensitive to attrition is consistent with the findings of Neumark and Kawaguchi 

(2004), who mimic the CPS sample design using the SIPP and conclude that the economic magnitude of bias 

induced by attrition, at least for some applications, is likely to be small. 

45 One exception is that, after dropping survey year 2019 observations, the distribution of remaining observations by 

year is much more similar across the treatment and control groups. 
24

sample experience more than one job loss over our (short) period of observation, suggesting that 

at least over this period the specific timing of job loss is not related to unobserved household 

characteristics. 

These results indicate that in practice, selection on attrition, COVID-19-related job loss, or 

duration until first observed job loss does not materially affect our estimates. Because we aren’t 

aware of other plausible explanations, we believe the differences in observable characteristics 

between the Job Loss and Subsequent Job Loss groups are likely attributable to random sampling 

error. This is especially plausible considering the small sample sizes of these groups. 

As a further check to quantify the scope of potential omitted variable bias, we use the 

methodology proposed by Oster (2019) to produce bounds on the estimated treatment effects of 

job loss presented in Table 2. An important assumption underlying this analysis is the extent to 

which selection on observed variables is informative about selection on unobserved variables.46

Results from this analysis (detailed in the Appendix) indicate that, under the assumption 

suggested by Oster (2019) that selection on unobservables is equal to selection on (carefully 

chosen) observables, the point estimate of the job loss effect on unbanked status is 0.110 in the 

Remain Employed specification and 0.171 in the Subsequent Job Loss specification. These point 

estimates are only about 12 percent and 3 percent smaller in magnitude than the estimates in 

Table 2, respectively. That these bounded treatment effect estimates are very close to the main 

estimate suggests that the scope of omitted variable bias is minimal. This is particularly true for 

the Subsequent Job Loss specification, and is consistent with our intuition that the treatment and 

control groups are likely similar in terms of unobservable characteristics. Both groups experience 

job loss; the main difference between the groups is just the timing of the job loss. 

4.5. Robustness

As additional robustness checks on our main estimation results in Table 2, we re-estimated 

the models using alternative definitions of job loss, including entry into unemployment for 

reasons especially likely to be involuntary, or entry into non-employment, regardless of reason 

(unemployed or out of the labor force). We find a similar pattern of results using those 

                                                            

46 Another important assumption is the value of “R௠௔௫”, the R-squared from a hypothetical regression of the 

outcome on treatment, observed controls, and unobserved controls. As described in the Appendix, we follow the 

suggestion from Oster (2019), to set R௠௔௫ equal to 1.3 * the R-squared from the regression specification with the 

treatment and control variables. 
25

alternative definitions (see Appendix Table A5).47 We also re-estimated the main specifications 

using probit; estimated marginal effects of job loss (in Appendix Table A6) are quite similar to 

the coefficient estimates using the linear probability models.48 

A remaining question we do not explore in this analysis is whether employment effects are 

symmetric, i.e., whether becoming employed increases a households’ likelihood of having a bank 

account. One challenge with such an analysis is that the unbanked population is much smaller, so 

it is difficult to make inferences due to small sample sizes. 

Taken together, the results presented in sections 4.4 and 4.5 show the main finding of the 

paper, that job loss leads to a large increase in the likelihood of being unbanked, is generally 

robust to a variety of sample selection criteria and empirical specifications. That these job loss 

effects are broad based within the sample and impact alternative outcomes in ways consistent 

with the pecuniary mechanism by which job loss should affect unbanked status further mitigates 

concern of bias in our estimator. 

5. DISCUSSION 

Expanding households’ access to the banking system has long been a priority of 

policymakers in the U.S. and abroad. Understanding the factors that affect households’ 

likelihood of opening and maintaining a bank account can help inform these efforts. This paper 

contributes to that understanding by estimating plausibly causal effects of a specific type of 

economic shock that has been posited to affect bank account ownership: job loss. 

We analyze data from biennial FDIC-sponsored supplements to the CPS from 2011 to 2019, 

linked to information on households’ work history from the basic monthly CPS in the months 

leading up to and subsequent to the FDIC survey. In our preferred specification, we identify the 

                                                            

47 In the CPS, unemployment can be attributed to “Job loser/ on layoff”, “Other job loser”, or “Temporary job 

ended”, which we term as involuntary, or else to “Job leaver”, “Re-entrant”, or “New-entrant”. We focus on 

unemployment for any reason, the definition used for the results presented in Table 2. This definition specifies that 

at minimum the individual is attempting to find new employment (as opposed to those out of the labor force) and 

therefore is more likely to have been financially affected, while at the same time not further reducing the sample size 

or being overly reliant on self-reported reasons for unemployment (as is the case with our “involuntary” 

unemployment definition). 

48 One concern with a linear probability model (relative to probit or logit) is that predicted effects may stray from the 

zero to one range implied by the binary outcome. This potential issue is most pronounced in cases where the sample 

mean is especially close to zero or one, which is not the case for our Remain Employed and Subsequent Job Loss 

samples (means of 0.158 and 0.241, respectively). For our main specifications, no predicted outcomes are greater 

than one and 9.4 and 11.3 percent (for the A and B samples respectively) fall below zero. 
26

job loss effect by estimating the likelihood of bank account ownership for a treatment group of 

households that become unemployed in the months leading up to the FDIC survey, compared to 

a control group of households that become unemployed one year later. By comparing households 

that experience a similar unemployment shock but that differ by the timing of the shock, the 

analysis mitigates concerns of potential selection bias in unobserved household characteristics 

associated with both job loss and bank account ownership status. We focus on low-income, 

renter households, a population likely to have little savings and more likely to be on the margin 

of having a bank account. 

Our main result is that job loss increases a household’s likelihood of being unbanked, and the 

magnitude of this job loss effect is large – about 75 percent of the mean unbanked rate in the 

sample. Effects are largest among the lowest income households in our sample, but are otherwise 

similar across other segments of the population (e.g. by race/ethnicity) and over time. We further 

show that the effects of job loss on being unbanked may persist for at least a year, but only 

among households that are not subsequently reemployed over that period. Most households 

experience employment shocks that are more transitory; these households are no more likely to 

be unbanked in the subsequent year. We also find that job loss leads to increased use of prepaid 

cards and certain nonbank products including money orders and check cashing services, 

suggesting that households may be using these products to substitute for (at least some of) the 

transaction services that a bank account provides. 

We acknowledge some challenges with our empirical analysis including the limited sample 

size and lack of longitudinal data on bank account ownership; these issues inhibit our ability to 

explore heterogeneity and preclude use of certain statistical techniques which might further 

establish the causal mechanism by which job loss affects unbanked status. We also note that 

households may be unbanked for reasons other than job loss, the focal mechanism of this paper. 

In particular, about half of unbanked households report that they have never had a bank account. 

The reasons that lead to such longer-term disengagement with the banking system may differ 

from the reasons why banked households become unbanked. Nonetheless, our focus on job loss 

suits the available data and our interpretation of unbanked outcomes as a transition, in principle, 

addresses a population more amenable to and experienced with banking. 

Regarding the scope of our findings, the incidence of job loss is substantial for the at-risk 

population of lower-income renter households we analyze. Further, households may be subject to 
27

other income or expense shocks (due to, e.g., changing work hours, health care expenses, loss of 

benefits, or other unexpected emergencies) which could similarly induce them to become 

unbanked.49 

Our results have direct implications for policymakers and other stakeholders interested in 

helping households open and maintain federally-insured depository accounts. For example, while 

temporary job loss does not necessarily lead to persistent loss of a bank account, it does 

contribute to intermittent unbanked status and leads to use of nonbank financial transaction and 

credit services. This transition may worsen a household’s financial circumstances at exactly the 

time when stability in accounts, payments, and credit access might be especially helpful in 

regaining a financial footing. Banks and other industry providers might alleviate such 

households’ transitory exits from account ownership, for example, by waiving minimum balance 

requirements or allowing households to carry a negative account balance without incurring 

overdraft fees. Many banks demonstrated a willingness to do so during the onset of the COVID19 pandemic.50 However these efforts are sometimes ad-hoc and typically require consumers to 

contact their financial institution to request a waiver, which may reduce take-up due to lack of 

awareness or other constraints. Regulatory agencies and industry groups could consider more 

proactive ways to extend such help, such as leveraging technology to identify and contact 

consumers that may be experiencing financial hardship due to job loss (such as those applying 

for unemployment benefits) or other adverse financial shocks. 

 

                                                            

49 While the incidence of economic shocks may vary over time (e.g., with macroeconomic conditions), based on the 

subjective life events data in the 2013 FDIC survey, about 10 percent of all households and 17 percent of the lowerincome renter households we analyze experienced a job loss within the previous year. For other types of shocks, 

FDIC (2014) shows that the incidence of significant income loss and significant increases in expenses were highest 

among households that became unbanked within the past year. And FDIC (2020) shows that unbanked rates are 

higher among households with monthly income that varies “somewhat” or “a lot” from month to month. 

50 For example, see the Bankrate.com article, “List of banks offering help to customers impacted by the 

coronavirus,” May 14, 2020. https://www.bankrate.com/banking/coronavirus-list-of-banks-offering-help-tocustomers-financial-hardship/ 
28

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31

Figure 1: Unbanked rate among U.S. households by year (percent)

Notes: Authors’ calculations using triennial data from the Survey of Consumer Finances (SCF) and biennial FDICsponsored supplements to the CPS (FDIC). In the SCF data, the unbanked rate is defined as the estimated proportion 

of households that do not have any transaction accounts, including checking, savings, and money market deposit 

accounts; money market mutual funds; and call or cash accounts at brokerages. The gray shaded areas indicate U.S. 

recessions as indicated by NBER (obtained from https://fred.stlouisfed.org/series/USRECD). 

Figure 2: Sample rotation structure of the CPS in months near the June FDIC surveys

Notes: The figure illustrates the sample rotation structure of the Current Population Survey (CPS) in the months near 

the June FDIC surveys, for each year indexed as t of 2011, 2013, 2015, and 2019. The table indicates the number of 

Months in Sample (MIS) each rotation group has participated in the CPS as of that calendar month (up to a 

maximum of 8 months, split into two, four-month sequences a year apart). Blank cells indicate that the rotation 

group is not included in the CPS in that calendar month. The red rectangle indicates the rotation groups used in the 

main analyses presented in this paper. 

 

Mar Apr May Jun Jul Aug Sep Mar Apr May Jun Jul Aug Sep Mar Apr May Jun Jul Aug Sep

1234 5678

1234 5678

1234 5678

1234 5678

1234 5678

1234 5678

1234 5678

1234 5678

FDIC supplement year ( t )

not observed Oct-Feb

Year after supplement ( t+1 )

Months in Sample

 Year before supplement ( t-1 )

not observed Oct-Feb
32

Figure 3: Treatment vs control groups, main specification 

Notes: This figure illustrates employment histories for the test and control groups for the main empirical 

specifications estimated in the paper. The values “E” (shaded green) and “U” (shaded red) indicate labor force status 

in the monthly CPS of employed and unemployed, respectively, while “*” cells (shaded gray) indicate that no 

selection criteria are applied to that rotation group/survey month. The red box indicates the month including the 

FDIC survey. To be included in the treatment group (Job Loss), at least one person in a household must satisfy the 

status “E” in the first month of observation (MIS=1) and “U” in the second month of observation (MIS=2). To be 

included in control group A (Remain Employed), all persons in the household who were employed in the first month 

of observation (MIS=1) must remain employed for the next three months (i.e. “E” in each month). To be included in 

control group B (Subsequent Job Loss), at least one person in a household must satisfy the status “E” in the fifth 

month of observation (MIS=5) and “U” in the sixth month of observation (MIS=6). All households must have at 

least one person employed in the first month of observation (MIS=1). Based on the individual job history criteria, 

the treatment and control group A households automatically satisfy the household employment requirement. For 

control group B, some individual in the household, not necessarily the individual experiencing job loss, must be 

employed in the first month of observation. 

Mar Apr May Jun Jul Aug Sep Mar Apr May Jun Jul Aug Sep

Treatment group: "Job Loss"

2 E U * * ****

3 EU * * ****

4E U * * ****

Control group A: "Remain Employed"

2 E E E E  

3 EE E E ** **

4E E E E ****

Control group B: "Subsequent Job Loss"

2 * * * * EU* *

3 ** * * EU* *

4* * * * EU* *

Rot Year after FDIC supplement (t+1 )

Grp

FDIC supplement year (t )

not observed Oct-Feb
33

Figure 4: Effect of job loss by rotation group in survey month 

A. Remain Employed control group 

B. Subsequent Job Loss control group 

Notes: This figure plots estimates of the job loss effect by rotation group, generated from OLS estimates of 

specifications that include a full interaction of the indicator for job loss with the categorical variable for rotation 

group. The specifications also include the full set of control variables listed in Appendix Table A2. The figure plots 

95% confidence intervals for each estimate. Panel A uses the Remain Employed control group and the sample 

includes all of the first four rotation groups, with a treatment sample size (for household job loss in month two of 

each rotation group) of 245, control sample size of 7,221, and total sample size of 7,466. Panel B uses the 

Subsequent Job Loss control group and the sample includes all of the first four rotation groups, with a treatment 

sample size (for household job loss in month two of each rotation group) of 245, control sample size of 123, and 

total sample size of 368. 
34

Table 1: Sample means 

Notes: Table presents sample means for the treatment and control groups from the main analyses presented in the 

paper. 

Treatment

Category Variable Job loss A. Remain Employed

B. Subsequent

Job Loss 

Outcomes Unbanked 0.324 0.153 0.097

Unbanked, longer-term 0.263 0.134 0.097

Unbanked, recently 0.056 0.014 0.000

Prepaid card 12 mo 0.227 0.129 0.120

Money order 12 mo 0.458 0.271 0.184

Check cash 12 mo 0.274 0.134 0.097

Pawn shop 12 mo 0.112 0.043 0.049

Payday loan 12 mo 0.034 0.034 0.029

Demographics Age 20 to 34 0.531 0.464 0.398

Age 35 to 54 0.425 0.449 0.505

Age 55 to 59 0.045 0.087 0.097

Female 0.559 0.554 0.573

White non-Hispanic 0.369 0.549 0.485

Hispanic, any race 0.307 0.228 0.340

Black non-Hispanic 0.251 0.153 0.097

Other race non-Hisp. 0.073 0.070 0.078

Native born 0.721 0.774 0.680

Married 0.279 0.257 0.417

Post secondary degree 0.240 0.268 0.291

Income and employment Self employed 0.095 0.075 0.087

Full time worker 0.480 0.690 0.660

Industry: Ag. and mining or const. 0.128 0.096 0.136

Industry: Manuf., utilities, or dist. 0.140 0.154 0.184

Industry: Retail or services 0.536 0.513 0.427

Industry: Educ., h'care, or gov't 0.196 0.237 0.252

Income < $20k 0.480 0.344 0.437

$20k <= Income < $40k 0.520 0.656 0.563

Number of adults 1.922 1.690 1.816

Number of employed adults 1.436 1.253 1.311

FDIC supplement info Year 2011 0.285 0.249 0.107

Year 2013 0.235 0.218 0.194

Year 2015 0.179 0.187 0.058

Year 2017 0.179 0.153 0.058

Year 2019 0.123 0.194 0.583

Rotation group 4 0.341 0.342 0.592

Rotation group 3 0.263 0.340 0.184

Rotation group 2 0.397 0.318 0.223

Number of observations 179 5409 103

Control
35

Table 2: Effect of job loss on probability of being unbanked 

Notes: Each column presents selected OLS estimates from a different specification. For each specification, “1(Job 

loss)” is an indicator for treatment. The listed value is the point estimate of β from Equation 1, with the standard 

error in parentheses. In Panel A, the control group consists of households that are employed in their first month in 

sample (MIS=1) and remain employed through the month of the FDIC survey (June). In Panel B, the control group 

consists of households that are employed in their 1st and 5th MIS and become unemployed in their 6th MIS. All 

specifications include fixed effects for survey year and rotation group. Other controls include demographics, income 

and employment characteristics. See Appendix Table A2 for the OLS estimates associated with the control 

variables. The symbol ** indicates the estimate is significant at the 5% level (* = 10%). 

 

Control group

(1) (2) (3) (4)

1(Job loss) 0.169 ** 0.125 ** 0.187 ** 0.177 **

(0.035) (0.034) (0.055) (0.055)

Effect as % of sample mean, dependent variable

107% 79% 78% 73%

Other controls N Y N Y

Mean, dependent variable 0.158 0.158 0.241 0.241

Number of observations 5,588 5,588 282 282

A. Remain Employed B. Subsequent Job Loss
36

Table 3: Heterogeneity in effects of job loss on probability of being unbanked 

Notes: Each column and panel (from (i) to (iv)) presents selected OLS estimates of a different empirical 

specification. In panel (i) the specifications include an interaction of the job loss indicator with a categorical 

measure of household income. In panel (ii) the interaction is with a categorical indicator of race/ethnicity. In panel 

(iii) the interaction is with the year of the FDIC survey. Interacted variables are also included on their own (not 

reported in the table). See Appendix Table A2 for control variables. 

Control group

(1) (2) (3) (4)

(i) By household Income (omitted: income < $20k)

1(Job loss) 0.229 ** 0.203 ** 0.310 ** 0.298 **

(0.054) (0.053) (0.074) (0.075)

1( . ) X 1($20k <= Income < $40k) -0.143 ** -0.148 ** -0.229 ** -0.226 **

(0.069) (0.067) (0.094) (0.094)

(ii) By race and ethnicity (omitted: White non-Hispanic)

1(Job loss) 0.184 ** 0.152 ** 0.197 ** 0.190 **

(0.055) (0.053) (0.069) (0.071)

1( . ) X Hispanic -0.107 -0.078 -0.138 -0.116

(0.085) (0.082) (0.115) (0.115)

1( . ) X Black 0.000 0.015 0.204 ** 0.211 **

(0.093) (0.088) (0.103) (0.103)

1( . ) X Other Race -0.134 -0.094 -0.114 -0.079

(0.113) (0.113) (0.119) (0.123)

(iii) By survey year (omitted: 2011)

1(Job loss) 0.163 ** 0.132 ** -0.056 -0.009

(0.066) (0.062) (0.159) (0.148)

1( . ) X 2013 0.006 -0.008 0.347 * 0.259

(0.100) (0.095) (0.183) (0.179)

1( . ) X 2015 0.050 0.029 0.399 ** 0.309 *

(0.109) (0.106) (0.183) (0.187)

1( . ) X 2017 -0.001 -0.027 0.225 0.227

(0.106) (0.096) (0.240) (0.239)

1( . ) X 2019 -0.040 -0.041 0.190 0.175

(0.111) (0.108) (0.195) (0.184)

Other controls N Y N Y

Mean, dependent variable 0.158 0.158 0.241 0.241

Number of observations 5,588 5,588 282 282

A. Remain Employed B. Subsequent Job Loss
37

Table 4: Persistence of the job loss effect on probability of being unbanked 

Notes: Each column presents selected OLS estimates of a different empirical specification. All specifications are 

estimated using the “persistence” sample as illustrated in Appendix Figure A5. In columns 3 and 4 the treatment 

group (“job loss previous year” is split into two mutually exclusive categories (aside from those missing due to 

attrition), based on whether the adult with the job loss was employed in the first month of the year that the 

household participates in the FDIC survey (i.e., in MIS=5). See Appendix Table A2 for control variables. 

Table 5: Effects of job loss on use of other financial products and services 

Notes: Each column and panel presents OLS estimates of a different empirical specification. The dependent variable 

of each specification is indicated at the top of each column, and indicates whether the household used the product or 

service within 12 months of the month of the FDIC survey. Use of prepaid cards is not observed in the 2011 FDIC 

survey, so data from 2011 are omitted for this regression. All specifications include the full set of control variables. 

See Table 2 for additional notes. 

Control group

(1) (2) (3) (4)

1(job loss previous year) 0.103 ** 0.059 *

(0.033) (0.032)

1(job loss previous year, not re-employed this year) 0.249 ** 0.194 **

(0.060) (0.057)

1(job loss previous year, re-employed this year) 0.005 -0.031

(0.036) (0.036)

Other controls N Y N Y

Mean, dependent variable 0.141 0.141 0.141 0.141

Number of observations 5,145 5,145 5,145 5,145

Remain Employed in Previous Year

Dependent variable

Prepaid

card

Nonbank 

money 

order

Nonbank 

check 

cashing

Pawn 

Shop

Loan

Payday

Loan

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

A. Control group: Remain Employed

1(Job loss) 0.086 ** 0.139 ** 0.115 ** 0.064 ** -0.002

(0.037) (0.037) (0.033) (0.024) (0.014)

Effect as % of sample mean 65% 50% 83% 142% -6%

Sample mean, dependent variable 0.132 0.277 0.139 0.045 0.034

Number of observations 4,192 5,588 5,588 5,588 5,588

B. Control group: Subsequent Job Loss

1(Job loss) 0.057 0.163 ** 0.095 * 0.061 0.005

(0.057) (0.065) (0.051) (0.045) (0.026)

Effect as % of sample mean 31% 46% 45% 69% 15%

Sample mean, dependent variable 0.182 0.358 0.209 0.089 0.032

Number of observations 220 282 282 282 282
38

Table 6: Effects of job loss on probability of being unbanked, by reasons for being 

unbanked 

Notes: Each column and panel presents selected OLS estimates from a different empirical specification. See text for 

definitions of the outcome variables. All specifications include the full set of control variables. 

Table 7: Effects of job loss on probability of being unbanked, by number of employed 

adults in the household 

Notes: Each column and panel presents selected OLS estimates from a different empirical specification. In panels (i) 

and (ii) the sample is stratified by the number of employed adults in the household. All specifications include the 

full set of control variables. See Table 2 for additional notes. 

 

Control group

(1) (2)

(i) Unbanked, main reason is Financial

1(Job loss) 0.098 ** 0.087 **

(0.029) (0.043)

Effect as % of sample mean 133% 63%

Sample mean, dependent variable 0.074 0.138

Number of observations 5,588 282

(ii) Unbanked, main reason is Non-financial

1(Job loss) 0.027 0.091 **

(0.025) (0.043)

Effect as % of sample mean 32% 88%

Sample mean, dependent variable 0.084 0.103

Number of observations 5,588 282

A. Remain Employed B. Subsequent Job Loss

Control group

(1) (2)

(i) One employed adult in household

1(Job loss) 0.138 ** 0.190 **

(0.042) (0.064)

Effect as % of sample mean 83% 74%

Sample mean, dependent variable 0.167 0.258

Number of observations 4,305 194

(ii) 2 or more employed adults in household

1(Job loss) 0.093 * 0.159

(0.055) (0.132)

Effect as % of sample mean 72% 77%

Sample mean, dependent variable 0.128 0.205

Number of observations 1,283 88

A. Remain Employed B. Subsequent Job Loss
39

Table 8: Person-level effects of job loss on probability of being unbanked 

Notes: Each column and panel presents selected OLS estimates from a different empirical specification. Unit of 

analysis is person-level. The indicator “job loss – self” is equal to 1 if the person suffered a job loss, and 0 

otherwise. The indicator “job loss – other” is equal to 1 if another adult in the household suffered a job loss, and 

equal to zero otherwise. All specifications include the full set of control variables, measured at the person level (as 

opposed to for a reference person in the household).

 

Control group

(1) (2)

(i) One employed adult in household

1(Job loss - self) 0.131 ** 0.176 **

(0.041) (0.073)

Effect as % of sample mean 45% 50%

Sample mean, dependent variable 0.289 0.350

Number of observations 6,441 214

(ii) 2 or more employed adults in household

1(Job loss - self) 0.181 ** 0.325 **

(0.057) (0.100)

Effect as % of sample mean 63% 79%

Sample mean, dependent variable 0.290 0.411

Number of observations 3,345 107

(iii) 2 or more employed adults in household; include job-loss indicator for other adults in household

1(Job loss - self) 0.186 ** 0.322 **

(0.057) (0.101)

1(Job loss - other) 0.115 ** -0.186

(0.051) (0.230)

Effect of job loss - self as % of sample mean 64% 78%

Effect of job loss - other as % of sample mean 40% -45%

Sample mean, dependent variable 0.290 0.411

Number of observations 3,345 107

A. Remain Employed B. Subsequent Job Loss
40

Table 9: Effects of job loss on probability of being unbanked, by recency of being 

unbanked 

Notes: Each column and panel presents selected OLS estimates from a different empirical specification where the 

control group is “Remain employed.” See text for definitions of the outcome variables. All specifications include the 

full set of control variables. 

Dependent variable

(1) (2)

(i) Main specification

1(Job loss) 0.038 ** 0.087 **

(0.017) (0.032)

Effect as % of sample mean 256% 63%

Sample mean, dependent variable 0.015 0.138

Number of observations 5,588 5,588

(ii) Persistence specification

1(job loss previous year) -0.005 0.053 *

(0.009) (0.031)

Effect as % of sample mean -41% 44%

Sample mean, dependent variable 0.013 0.123

Number of observations 5,145 5,145

Unbanked

recently

Unbanked,

longer-term
41

Table 10: Effects of job loss on probability of being unbanked, alternative samples 

Notes: Each column and panel presents selected OLS estimates from a different empirical specification. All 

specifications include the full set of control variables. In panel C the alternative analysis sample is relevant only for 

the Subsequent Job Loss control group. See text for descriptions of the alternative analysis samples. Sample means 

for the alternative analysis samples are presented in Appendix Table A4. 

Control Group A. Remain Employed B. Subsequent Job Loss

(i) No Attrition 

1(Job loss) 0.093 * 0.119 *

(0.048) (0.062)

Effect as % of sample mean 67% 70%

Sample mean, dependent variable 0.140 0.171

Number of observations 3,086 170

(ii) Drop Survey Year 2019

1(Job loss) 0.128 ** 0.203 **

(0.036) (0.074)

Effect as % of sample mean 76% 69%

Sample mean, dependent variable 0.170 0.295

Number of observations 4,517 200

(iii) Include HHs not employed in first month-in-sample

1(Job loss) 0.168 **

(0.052)

Effect as % of sample mean 68%

Sample mean, dependent variable 0.248

Number of observations 306
42

APPENDIX 

Following Oster (2019), we provided further evidence of robustness to omitted variable bias 

under the assumption that the relationship between treatment and unobservables can be 

recovered from the relationship between the treatment and observables. For this analysis, we 

make use of our estimates for the specifications in Table 2, both with and without controls. 

Specifically, we use the coefficient estimates for β in each specification as well as the R-squared 

term from the model with controls. 

The Oster methodology makes use of the change in coefficient value after controls are added 

as well as assumptions for the R-squared from a hypothetical regression of the outcome on 

treatment and both the observed and unobserved controls, termed R௠௔௫. As we discuss in 

Section 4.2, the coefficient estimates do not attenuate drastically once controls are added, 

especially for specifications using the Subsequent Job Loss control group. For a maximum Rsquared, Oster suggests using R௠௔௫ ൌ ΠRଶ, where Rଶ is from the specification with observed 

controls and Π ൌ 1.3, based on an assumption that 90 percent of analyses using a randomized 

treatment should survive (Oster 2019). The final component of the bounding calculation is an 

assumption for the relative degree of selection on observed and unobserved variables, termed δ. 

The Oster (2019) analysis is not specifically designed for models with a binary outcome. 

However, we find that the magnitude of our estimates is not sensitive to using a probit model, 

rather than a linear probability model, so we expect that this aspect of model choice is of lesser 

importance for interpreting our results (see section 4.5 and Appendix Table A6). For further 

intuition, see Oster (2019), where the restricted estimator is defined on p. 192. 

In Appendix Table A7 panels (i), (ii), and (iii), we provide the uncontrolled and controlled 

inputs to the calculations as well as the bounding estimates for our treatment effect estimates 

under a range of reasonable assumptions for δ (which cannot be known).1

 A typical assumption, 

recommended in Oster (2019), is δ ൌ 1, where carefully-chosen observables are assumed to be 

equally informative as unobservables. We also include bounding estimates for δ ൌ 0.5, where 

observables are twice as informative, and δ ൌ 2, where unobservables are twice as informative. 

In panel A, for the Remain Employed control, we show that the treatment effect estimated as 

                                                            

1

 We use the Stata module psacalc (Oster 2013), with parameter inputs for δ and R௠௔௫ as specified in Table 11 

and with the survey year and rotation group indicators entered as unrelated controls to be included in all regressions 

(similar to our approach in Table 2, where all specifications include survey year and rotation group indicators). 
43

0.125 in Table 2, would be bounded at 0.118, 0.110, and 0.095 under the least, middle, and most 

conservative scenarios. The estimate would go to zero at δ ൌ 7.4, which is quite large. There is 

even less attenuation for the estimates in panel B, for the Subsequent Job Loss control. The 

estimate of 0.177 from Table 2 would be bounded at 0.174, 0.171, and 0.165 under three 

scenarios and would only go to zero at δ ൌ 9.6. The lesser movement of bounding estimates in 

panel B can be explained by the more modest attenuation of coefficient estimates once controls 

are added and to the higher Rଶ in the controlled regression (relative to panel A). While estimates 

for both controls survive this bounding analysis of omitted variable bias, the apparently less 

sensitive results from the Subsequent Job Loss estimates are perhaps indicative of the greater 

similarity of the treatment group to that control, especially in terms of factors that cannot be 

observed. 

APPENDIX REFERENCES 

Oster, Emily. 2013. “PSACALC: Stata Module to Calculate Treatment Effects and Relative 

Degree of Selection Under Proportional Selection of Observables and Unobservables.” 

Statistical Software Components S457677, Boston College Department of Economics, 

revised 18 Dec 2016. 

 
44

Appendix Figure A1: Unbanked rates (percent) by selected household characteristics, 2019 

Notes: Authors’ computations using 2019 FDIC survey and CPS; estimates are weighted using household 

supplement weights. See FDIC 2020 for more details. 

Appendix Figure A2: Effect of job loss by household income 

A. Remain Employed control group B. Subsequent Job Loss control group 

Notes: This figure plots estimates and 95% confidence intervals of the job loss effect by household income, 

generated from OLS estimates of a specification that includes a full interaction of the indicator for job loss with a 

categorical indicator for household income. See Table 3 panel (i) for the point estimates on the interacted terms. The 

specifications also include the full set of control variables listed in Appendix Table A2. Panel A uses the Remain 

Employed control group and Panel B uses the Subsequent Job Loss control group. 

 
45

Appendix Figure A3: Effect of job loss by race and ethnicity 

A. Remain Employed control group B. Subsequent Job Loss control group 

Notes: This figure plots estimates and 95% confidence intervals of the job loss effect by race and ethnicity, 

generated from OLS estimates of a specification that includes a full interaction of the indicator for job loss with a 

categorical indicator of race/ethnicity. See Table 3 panel (ii) for the point estimates on the interacted terms. The 

specifications also include the full set of control variables listed in Appendix Table A2. Panel A uses the Remain 

Employed control group and Panel B uses the Subsequent Job Loss control group.

Appendix Figure A4: Effect of job loss by survey year 

A. Remain Employed control group B. Subsequent Job Loss control group 

Notes: This figure plots estimates and 95% confidence intervals of the job loss effect by race and ethnicity, 

generated from OLS estimates of a specification that includes a full interaction of the indicator for job loss with a 

categorical indicator for FDIC survey year. See Table 3 panel (iii) for the point estimates on the interacted terms. 

The specifications also include the full set of control variables listed in Appendix Table A2. Panel A uses the 

Remain Employed control group and Panel B uses the Subsequent Job Loss control group.

 
46

Appendix Figure A5: Treatment vs control groups, “Persistence” specification 

Notes: This figure illustrates the test and control group for the Persistence specification estimated in the paper. The 

values “E” (shaded green) and “U” (shaded red) indicate labor force status in the monthly CPS of employed and 

unemployed, respectively, while “*” cells (shaded gray) indicate that no criteria are applicable for that rotation 

group/survey month. The red box indicates the month including the FDIC survey. To be included in the Treatment 

group (Job Loss Previous Year), at least one person in a household must satisfy the status “E” in the first month of 

observation (MIS=1) and “U” in the second month of observation (MIS=2). To be included in Control group 

(Remain Employed Previous Year), all persons in the household who were employed in the first month of 

observation (MIS=1) must remain employed for the next three months (i.e. “E” in each month). In contrast to Figure 

3, which is based on three rotation groups (2, 3, and 4), the Persistence sample is based on four rotation groups (5, 6, 

7, and 8). 

 

Mar Apr May Jun Jul Aug Sep Mar Apr May Jun Jul Aug Sep

Treatment group: "Job Loss Previous Year"

5 EU* * * ***

6 EU* * * * * *

7 EU* * * * * *

8E U * * * * * *

Control group: "Remain Employed Previous Year"

5 EEEE * ***

6 EEEE * * * *

7 EEEE ** * *

8E E E E * * * * not observed Oct-Feb

Rot Year before supplement (t-1 ) FDIC supplement year (t )

Grp
47

Appendix Table A1: Description of variables used in the analysis 

(continued on next page) 

 

Category Variable Source Fields and values Description

Linking Household FDIC, 

CPS

hrhhid, hrhhid2 Household identifiers

Person CPS cpsidp Person identifier, pulineno used for linking to 

person-level BFS file

Outcomes Unbanked FDIC hunbnk=="Unbanked", pes2a Indicator for household not owning a bank 

account (pes2a is used to create a personlevel level indicator of bank account 

ownership status)

Unb. Always FDIC hbnkprevly Indicator for always unbanked (zero 

otherwise)

Unbanked, longer-term FDIC hbnkprevly Indicator for long-term unbanked, less than 

a year (zero otherwise)

Unbanked, recently FDIC hbnkprevly Indicator for long-term unbanked, a year or 

more (zero otherwise)

Prepaid card 12 mo FDIC use12pp Indicator for using a prepaid card (zero 

otherwise and missing in 2011)

Money order 12 mo FDIC use12mo Indicator for using a money order (zero 

otherwise)

Check cash 12 mo FDIC use12cc Indicator for using check cashing (zero 

otherwise)

Pawn shop 12 mo FDIC use12pw Indicator for using a pawn shop loan (zero 

otherwise)

Payday loan 12 mo FDIC use12pd Indicator for using a payday loan (zero 

otherwise)

Treated, job loss mo 2 CPS empstat: 10-12 Household transition of employed (MIS=1) 

to not employed (MIS=2)

Treated, unemp mo 2 CPS empstat: 10-12, whyunemp: 1-6 Household transition of employed (MIS=1) 

to unemployed (MIS=2) (any reason)

Treated, invol unemp mo2 CPS empstat: 10-12, whyunemp: 1-3 Household transition of employed (MIS=1) 

to involuntary unemployed (MIS=2) (see 

footnote in main text)

Reason unb. Financial FDIC hunbnkrm, hunbnkrmv2, 

hunbnkrmv3

Indicator for unbanked due to financerelated reasons (see footnote in main text)

Reason unb. Other FDIC hunbnkrm, hunbnkrmv2, 

hunbnkrmv3

Indicator for unbanked due to all other 

reasons, as well as non-reponse regarding 

reasons (see footnote in main text)

Labor force, mo 5 CPS empstat: 10-12, whyunemp: 1-6 Indicator for employed or unemployed in 

MIS=5

Employed, mo 5 CPS empstat: 10-12 Indicator for employed in MIS=5
48

Appendix Table A1 [continued] 

Note: FDIC refers to the FDIC supplement to the CPS; source is the multiyear data file (hh_multiyear_analys.csv, 

available at https://www.fdic.gov/analysis/household-survey/). CPS revers to the basic monthly files of the 

Current Population Survey. The source is IPUMS CPS (available at https://cps.ipums.org/cps/index.shtml). 

Category Variable Source Fields and values Description

Demo. Age 20 to 34 CPS age>=20 & age<35 Indicator, reference person, month 1

Age 35 to 54 CPS age>=35 & age<55 Indicator, reference person, month 1

Age 55 to 60 CPS age>=55 & age<60 Indicator, reference person, month 1

Female CPS sex=2 Indicator, reference person, month 1

White non-Hispanic CPS race==100 & hispan==0 Indicator, reference person, month 1

Hispanic, any race CPS hispan>0 Indicator, reference person, month 1

Black non-Hispanic CPS hispan==0 & race==200 Indicator, reference person, month 1

Other race non-Hisp. CPS hispan==0 & race!=100 & 

race!=200

Indicator, reference person, month 1

Native born CPS bpl=9900 Indicator, reference person, month 1

Married CPS marst==1 Indicator, reference person, month 1

Post secondary degree CPS educ>=91 Indicator, Associate's degree or higher, 

reference person, month 1

Inc. & emp. Self employed CPS classwkr==13 | classwkr==14 Indicator, first person employed, month 1)

Full time worker CPS wkstat==11 Indicator, first person employed, month 1)

Second job CPS multjob==2 Indicator, first person employed, month 1)

Industry: Ag. and mining or const. CPS ind: 0170-0490, 0770 Indicator, first person employed, month 1)

Industry: Manuf., utilities, or dist. CPS ind: 0570-0690, 1070-3990, 

4070-4590, 6070-6390

Indicator, first person employed, month 1)

Industry: Retail or services CPS ind: 4670-5790, 6470-7070, 

7080-7790, 8560-9290

Indicator, first person employed, month 1)

Industry: Educ., h'care, or gov't CPS ind: 7860-8470, 9370-9890 Indicator, first person employed, month 1)

Income < $20k CPS faminc>=100 & faminc<=500 Indicator, household, month 1

$20k <= Income < $40k CPS faminc>=600 & faminc<=730 Indicator, household, month 1

40,000 - 59,999 CPS faminc>=740 & faminc<=820 Indicator, household, month 1

60,000 - 99,999 CPS faminc>=830 & faminc<=841 Indicator, household, month 1

100,000 - 149,999 CPS faminc==842 Indicator, household, month 1

150,000 and over CPS faminc==843 Indicator, household, month 1

Homeowners CPS hhtenure==1 Indicator, household, month 1

Number of adults CPS pernum, age Number persons age 20 to 59, month 1

Number of employed adults CPS empstat Number persons employed age 20 to 59, 

month 1

Survey Year 2011 FDIC hryear4 Indicator, FDIC supplement year

Year 2013 FDIC hryear4 Indicator, FDIC supplement year

Year 2015 FDIC hryear4 Indicator, FDIC supplement year

Year 2017 FDIC hryear4 Indicator, FDIC supplement year

Year 2019 FDIC hryear4 Indicator, FDIC supplement year

Rotation group 4 CPS mish==4 Indicator, supplement in month 4

Rotation group 3 CPS mish==3 Indicator, supplement in month 3

Rotation group 2 CPS mish==2 Indicator, supplement in month 2

Rotation group 1 CPS mish==1 Indicator, supplement in month 1
49

Appendix Table A2: Selection into treatment 

(continued on next page) 

A. Remain 

Employed

B. Subsequent 

Lob Loss

Age 20 to 34 0.004 0.052

(0.005) (0.054)

Age 55 to 59 -0.008 0.084

(0.007) (0.112)

Female -0.001 -0.043

(0.005) (0.059)

Hispanic, any race 0.020** 0.041

(0.008) (0.075)

Black non-Hispanic 0.032*** 0.166**

(0.008) (0.074)

Other race non-Hisp. 0.009 0.058

(0.009) (0.104)

Native born 0.003 0.033

(0.008) (0.076)

Married -0.002 -0.105*

(0.006) (0.062)

Post secondary degree 0.003 -0.003

(0.005) (0.056)

Self employed 0.007 -0.038

(0.011) (0.094)

Full time worker -0.027*** -0.093*

(0.006) (0.053)

Industry: Ag. and mining or const. 0.017 0.117

(0.011) (0.100)

Industry: Manuf., utilities, or dist. 0.007 0.122

(0.007) (0.091)

Industry: Retail or services 0.005 0.137**

(0.006) (0.066)

$20k <= Income < $40k -0.014** 0.023

(0.005) (0.058)

Control group
50

Appendix Table A2 [continued] 

Each column presents OLS estimates from a different specification, explaining the treatment variable in terms of 

control variables for each control group. The first column presents estimates explaining job loss in terms of control 

variables for the treatment group and control group A. The second column presents estimates explaining job loss in 

terms of control variables for the treatment group and control group B. See Table 1 for definitions of omitted 

categorical variables. The symbol *** indicates the estimate is significant at the 1% level (** = 5%; * = 10%).

 

A. Remain 

Employed

B. Subsequent 

Lob Loss

Number of adults 0.004 0.004

(0.004) (0.040)

Number of employed adults 0.019*** 0.07

(0.007) (0.049)

Year 2013 -0.005 -0.147*

(0.007) (0.076)

Year 2015 -0.006 -0.005

(0.007) (0.082)

Year 2017 0.001 0.039

(0.008) (0.075)

Year 2019 -0.012* -0.483***

(0.007) (0.078)

Rotation group 4 -0.01 -0.105

(0.006) (0.069)

Rotation group 3 -0.015** -0.022

(0.006) (0.068)

R-squared 0.02 0.321

Number of observations 5,588 282

Control group
51

Appendix Table A3: Full OLS Estimation Results, Main Specifications 

(continued on next page) 

A. Remain 

Employed

B. Subsequent Job 

Loss

1(Job loss) 0.125*** 0.177***

(0.0337) (0.0553)

Age 20 to 34 -0.0141 0.0135

(0.0101) (0.0534)

Age 55 to 59 -0.0455*** -0.0835

(0.0155) (0.0834)

Female 0.0145 0.0851

(0.00947) (0.0533)

Hispanic, any race 0.130*** 0.179**

(0.0145) (0.0727)

Black non-Hispanic 0.143*** 0.153**

(0.0153) (0.0736)

Other race non-Hisp. 0.00221 0.00307

(0.0173) (0.0835)

Native born -0.00288 0.137*

(0.0140) (0.0696)

Married -0.00346 -0.00368

(0.0123) (0.0539)

Post secondary degree -0.0920*** -0.0941*

(0.00881) (0.0504)

Self employed -0.0234 0.0586

(0.0177) (0.0914)

Full time worker -0.00767 0.00830

(0.0105) (0.0513)

Industry: Ag. and mining or const. 0.147*** 0.167*

(0.0213) (0.0968)

Industry: Manuf., utilities, or dist. 0.00737 0.0370

(0.0148) (0.0784)

Industry: Retail or services 0.0392*** 0.0969

(0.0108) (0.0641)

$20k <= Income < $40k -0.0859*** -0.123**

(0.0109) (0.0552)

Control group
52

Appendix Table A3 [continued] 

Notes: This table presents OLS estimates on all control variables for the specifications in Table 2 of the 

paper. See Table 1 for definitions of omitted categorical variables. The symbol *** indicates the estimate is 

significant at the 1% level (** = 5%; * = 10%). See Table 2 for additional notes. 

 

A. Remain 

Employed

B. Subsequent Job 

Loss

Number of adults 0.0297*** 0.0871**

(0.00819) (0.0418)

Number of employed adults -0.0456*** -0.0787

(0.0111) (0.0537)

Year 2013 0.0278** -0.0416

(0.0142) (0.0806)

Year 2015 0.00712 -0.0299

(0.0144) (0.0945)

Year 2017 -0.00163 -0.0661

(0.0149) (0.0870)

Year 2019 -0.0300** -0.0668

(0.0133) (0.0794)

Rotation group 4 0.00886 0.0857

(0.0113) (0.0595)

Rotation group 3 0.0170 0.115

(0.0115) (0.0719)

Constant 0.156*** -0.175

(0.0262) (0.144)

R-squared 0.108 0.210

Number of observations 5,588 282

Control group
53

Appendix Table A4: Sample means of treatment and control groups, alternative samples 

Notes: Table presents sample means for alternative sample selection criteria. In Panel A the sample excludes 

households with any persons that attrite during any of the eight months-in-sample. In Panel B the sample excludes 

all observations from survey year 2019. In Panel C the Subsequent Job Loss control group does not exclude 

households with no employed adults in the first month-in-sample (MIS); the Job Loss treatment group is identical to 

the group used in the main analysis. 

 

Treatment Treatment

Variable Job Loss Remain 

Employed

Subsequent

Job Loss Job Loss Remain 

Employed

Subsequent

Job Loss Job Loss

Subsequent

Job Loss

Unbanked 0.272 0.140 0.079 0.338 0.170 0.140 0.324 0.142

Unbanked, longer-term 0.198 0.125 0.079 0.268 0.148 0.140 0.263 0.134

Unbanked, recently 0.074 0.011 0.000 0.064 0.017 0.000 0.078 0.055

Prepaid card 12 mo 0.203 0.126 0.127 0.245 0.137 0.125 0.227 0.115

Money order 12 mo 0.469 0.272 0.213 0.497 0.298 0.233 0.458 0.236

Check cash 12 mo 0.198 0.129 0.101 0.299 0.148 0.140 0.274 0.118

Pawn shop 12 mo 0.086 0.037 0.045 0.115 0.050 0.070 0.112 0.071

Payday loan 12 mo 0.049 0.035 0.022 0.038 0.036 0.047 0.034 0.031

Age 20 to 34 0.444 0.387 0.360 0.554 0.484 0.419 0.531 0.449

Age 35 to 54 0.494 0.505 0.539 0.414 0.444 0.558 0.425 0.465

Age 55 to 59 0.062 0.109 0.101 0.032 0.072 0.023 0.045 0.087

Female 0.556 0.557 0.596 0.567 0.555 0.535 0.559 0.591

White non-Hispanic 0.370 0.547 0.506 0.350 0.533 0.512 0.369 0.496

Hispanic, any race 0.321 0.231 0.315 0.325 0.232 0.302 0.307 0.307

Black non-Hispanic 0.259 0.152 0.112 0.248 0.163 0.140 0.251 0.126

Other race non-Hisp. 0.049 0.070 0.067 0.076 0.072 0.047 0.073 0.071

Native born 0.704 0.758 0.708 0.713 0.767 0.698 0.721 0.701

Married 0.321 0.274 0.371 0.261 0.250 0.488 0.279 0.378

Post secondary degree 0.284 0.271 0.270 0.236 0.263 0.209 0.240 0.283

Self employed 0.099 0.089 0.079 0.102 0.070 0.140 0.095 0.071

Full time worker 0.506 0.692 0.640 0.452 0.675 0.651 0.480 0.535

Industry: Ag. and mining or const. 0.086 0.104 0.112 0.127 0.094 0.186 0.128 0.118

Industry: Manuf., utilities, or dist. 0.160 0.152 0.202 0.115 0.149 0.140 0.140 0.181

Industry: Retail or services 0.494 0.501 0.449 0.561 0.524 0.326 0.536 0.402

Industry: Educ., h'care, or gov't 0.259 0.244 0.236 0.197 0.233 0.349 0.196 0.228

Industry: Not observed 0.000 0.000 0.000 0.000 0.000 0.000 0.000 0.071

Income < $20k 0.481 0.340 0.427 0.490 0.370 0.558 0.480 0.528

$20k <= Income < $40k 0.519 0.660 0.573 0.510 0.630 0.442 0.520 0.472

Number of adults 1.889 1.617 1.753 1.936 1.700 2.047 1.922 1.787

Number of employed adults 1.370 1.219 1.292 1.452 1.258 1.302 1.436 1.063

Year 2011 0.272 0.250 0.112 0.325 0.309 0.256 0.285 0.181

Year 2013 0.198 0.216 0.191 0.268 0.270 0.465 0.235 0.181

Year 2015 0.160 0.189 0.067 0.204 0.231 0.140 0.179 0.102

Year 2017 0.222 0.153 0.067 0.204 0.190 0.140 0.179 0.047

Year 2019 0.148 0.192 0.562 0.000 0.000 0.000 0.123 0.488

Rotation group 4 0.333 0.339 0.562 0.338 0.343 0.279 0.341 0.543

Rotation group 3 0.247 0.348 0.191 0.274 0.338 0.233 0.263 0.213

Rotation group 2 0.420 0.313 0.247 0.389 0.319 0.488 0.397 0.244

Number of observations 81 3005 89 157 4517 43 179 127

A. No Attrition B. Drop Survey Year 2019

Control Control

C. Include HHs not 

employed in first MIS
54

Appendix Table A5: Alternative definitions of job loss 

Notes: Each column presents selected OLS estimates from a different specification. See Table 2 for definitions of 

Panel A and B in terms of the timing of job loss. Panel (i) repeats the main result, where job loss is defined as entry 

into unemployment. Panel (ii) defined job loss as an entry into unemployment where the reason given indicates that 

unemployment is especially likely to be involuntary. Panel (iii) defines job loss as entry into nonemployment 

(unemployed or not in labor force). All specifications include fixed effects for FDIC survey year and rotation group. 

Other controls include demographics, income and employment characteristics. Panel (i) repeats results from Table 2, 

where job loss is defined. See Appendix Table 2 for the OLS estimates associated with the control variables. The 

symbol ** indicates the estimate is significant at the 5% level (* = 10%). 

 

 

Control group

(1) (2) (3) (4)

(i) Main result, job loss to unemployment

1(Job loss to unemp.) 0.169 ** 0.125 ** 0.187 ** 0.177 **

(0.035) (0.034) (0.055) (0.055)

Effect as % of sample mean, dependent variable

107% 79% 78% 73%

Other controls N Y N Y

Mean, dependent variable 0.158 0.158 0.241 0.241

Number of observations 5,588 5,588 282 282

(ii) Alternative treatment, job loss to unemployment (involuntary)

1(Job loss) 0.195 ** 0.155 ** 0.195 ** 0.206 **

(0.041) (0.039) (0.065) (0.067)

Effect as % of sample mean, dependent variable

124% 99% 80% 84%

Other controls N Y N Y

Mean, dependent variable 0.157 0.157 0.246 0.246

Number of observations 5,543 5,543 228 228

(iii) Alternative treatment, job loss to nonemployment (unemployed or out of the labor force)

1(Job loss) 0.147 ** 0.118 ** 0.119 ** 0.110 **

(0.023) (0.022) (0.037) (0.037)

Effect as % of sample mean, dependent variable

90% 73% 48% 44%

Other controls N Y N Y

Mean, dependent variable 0.163 0.163 0.248 0.248

Number of observations 5,819 5,819 601 601

A. Remain Employed B. Subsequent Job Loss
55

Appendix Table A6: Probit estimates of Effect of job loss on probability of being unbanked 

Notes: Each column presents selected probit estimates from a different specification. For each specification, “1(Job 

loss)” is an indicator for treatment. The listed value is the point estimate of β from Equation 1, with the standard 

error in parentheses. In Panel A, the control group consists of households that are employed in their first month in 

sample (MIS=1) and remain employed through the June FDIC survey. In Panel B, the control group consists of 

households that are employed in their 1st and 5th MIS and become unemployed in their 6th MIS. All specifications 

include fixed effects for FDIC survey year and rotation group. Other controls include demographics, income and 

employment characteristics. The symbol ** indicates the estimate is significant at the 5% level (* = 10%). 

 

Control group

(1) (2) (3) (4)

1(Job loss) 0.559 ** 0.442 ** 0.708 ** 0.795 **

(0.100) (0.106) (0.221) (0.243)

Marginal effect of Job Loss

at Job loss=1 0.318 0.235 0.299 0.258

(0.035) (0.032) (0.038) (0.039)

at Job loss=0 0.151 0.122 0.108 0.074

(0.005) (0.005) (0.033) (0.028)

difference (1 vs 0) 0.167 ** 0.113 ** 0.191 ** 0.183 **

(0.035) (0.032) (0.054) (0.050)

difference Chi2

 statistic 22.580 12.166 12.627 13.232

Other controls N Y N Y

Mean, dependent variable 0.158 0.158 0.241 0.241

Number of observations 5,588 5,588 282 282

A. Remain Employed B. Subsequent Job Loss
56

Appendix Table A7: Bounding analysis of omitted variable bias (Oster 2019) 

Notes: Each column and panel presents selected OLS estimates from a different empirical specification. See the 

Appendix for definitions as well as discussion of the Oster (2019) parameters.

Control group A. Remain Employed B. Subsequent Job Loss

(1) (2)

(i) Estimates without other controls

1(Job loss) 0.169 0.187

(0.035) (0.055)

R-squared 0.013 0.088

(ii) Estimates including other controls

1(Job loss) 0.125 0.177

(0.034) (0.055)

R-squared 0.108 0.210

(iii) Bounding estimates (Oster 2019)

1(Job loss) | δ=0.5, Rmax 0.118 0.174

1(Job loss) | δ=1.0, Rmax 0.110 0.171

1(Job loss) | δ=2.0, Rmax 0.095 0.165

R-squared max. (Rmax) 0.140 0.273

Mean, dependent variable 0.158 0.241

Number of observations 5,588 282