The Impact of the Gig-Economy on Financial Hardship among
Low-Income Families
Abstract
Problem Definition: New work arrangements coordinated by gig-economy platforms offer workers discretion over their work schedules at the expense of traditional worker protections. We
empirically measure the impact of expanding access to gigs on worker financial health, with a
focus on low- and moderate-income (LMI) families.
Academic/Practical Relevance: Understanding the welfare implication of access to gigs informs
workers considering working gigs and regulators empowered to protect them. Additionally, firms
who rely on this working arrangement may find themselves exposed to increased worker turnover
and regulatory intervention if gigs negatively impact worker financial health.
Methodology: We analyze a novel data set documenting the financial health of a sample of
LMI families. We are interested in the likelihood that a family experiences hardship, meaning
they fail to pay their bills on time. We leverage the sequential launch of Uber’s UberX service
across locations to identify the impact of the associated increase in access to gigs on hardship
via a difference-in-differences design. The granularity of our data allows exploration of possible
mechanisms for our results.
Results: We find that UberX increases hardship among the LMI population, primarily by decreasing overall take-home pay (i.e. annual income less expenses). This is despite a corresponding reduction in income volatility, generally a boon to LMI families who have insufficient savings
to weather unexpected dips in earnings.
Managerial Implications: These results caution that gigs can be harmful to the most vulnerable members of society. Our analysis of antecedents of this result offers guidance for effective
mechanisms for improving worker financial health in the presence of gigs. Further, we find that
gigs offer potential benefits to the LMI population through reduction in income volatility.

Keywords— gig-economy, Uber, econometric analysis, service operations, public policy

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 1

Introduction

On-demand peer-to-peer services (‘gigs’) coordinated by platforms like Uber, Lyft, and Postmates
rely on independent workers to provide service. Independent workers enjoy complete control over
their work schedules. Workers may use this autonomy to schedule gig work around their existing
day jobs to supplement their income, or workers may use gigs as a substitute for more conventional
forms of work to better integrate their work with other responsibilities. The drawback of this
independence is the lack of traditional employment protections. In particular, worker autonomy
over work hours makes infeasible minimum hourly wage guarantees. Instead platforms pay workers
per completed service, so the amount a worker earns depends on the number of consumers seeking
service. For example, an hour spent driving for Uber may be a lucrative use of time on a busy
night but may not even cover expenses on a slow afternoon. The absence of worker protections
from this business model has provoked a string of lawsuits aimed at Uber and Postmates (Lien,
2016; Bhardwaj, 2018) and skepticism that gigs improve worker welfare (McCabe and Devaney,
2015).
The aim of this paper is to understand the impact the gig economy has on worker welfare. In
addition to informing workers’ choices about participating in the gig economy, our analysis should
attract the attention of firms who are increasingly organizing their operations around independent
workers. The worker welfare associated with this arrangement impacts worker turnover, as well
as the likelihood that regulators intervene. For example, New York City has considered enforcing
a minimum hourly wage for ride-share drivers (Siddiqui, 2018) and recently imposed a cap on
ride-share drivers (Shapiro, 2018) in the name of driver welfare.
We focus on a specific dimension of welfare, which we call financial hardship. A family experiences financial hardship when it fails to pay its bills on time. Though this measure is related
to more accessible indicators of financial stability, like annual income, a family whose income is
volatile may appear to be financially stable (i.e. annual income > annual expenses) while still
experiencing transient financial hardship. This is particularly likely for families with few savings
to draw on in months when expenses exceed earnings.
We empirically study changes in financial hardship following an expansion of access to gigs.
We employ a novel data set documenting survey responses to detailed questions about low- and

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 moderate-income families’ financial security. These data include an explicit measure of financial
hardship, as well as granular information about potential antecedents to hardship. In particular,
we conceptualize hardship as a function of the long-run average income earned by a family, the
volatility of that income over time, the long-run average expenses of a family, and the volatility
of expenses. The richness of our data allows for exploration of not only steady-state causes of
hardship (e.g. annual income and expenses) but also transient causes of hardship (e.g. month-tomonth variability in income and unexpected expenses).
We center our analysis on low- and moderate-income (LMI) households for two reasons. First,
this population is likely to experience a financial hardship, so a change in the likelihood of financial
hardship resulting from access to gigs is highly relevant to this population. This population is also
more likely to work gigs than their higher-income counterparts (Smith, 2016). Taken together,
changes in financial health resulting from access to gigs are likely to have the largest impact on the
population we study.
Gigs represent an opportunity for families to improve their financial health both by increasing
income and reducing income volatility. The flexibility of gigs allows workers to work in their spare
time, theoretically allowing workers to increase the time they spend earning, increasing income.
Additionally, the flexibility of gigs allows workers to adjust to shocks in other sources of income.
For example, a worker who receives fewer shifts than usual at his day job may supplement his
income by spending those hours working for Uber. In doing so, the worker avoids finding himself
with insufficient funds to pay his bills at the end of the month. These positive effects should have
the greatest impact on low-income families, who have the greatest need to supplement their income
and are more likely to experience unpredictable work schedules (White, 2015).
Gigs also have the potential to reduce worker financial health by reducing worker security. Gig
workers do not enjoy a minimum hourly wage guarantee, meaning gig work may not pay as well
as a conventional alternative. Furthermore, the dependence of gig-pay on demand for gig-service
may introduce income volatility. As the demand for services fluctuates, so too does the worker’s
pay. These potentially damaging effects are relevant to the extent that workers substitute gig-work
for conventional employment options. Workers in other contexts have demonstrated a willingness
to trade control of their time at the expense of financial gain (Smithson et al., 2004). Members of
low-income households may be especially eager to make this trade: low-skill, low-wage workers have
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 less access to flexibility at work than their high-skill, high-wage counterparts (Bond and Galinsky,
2011). Additionally, gigs may damage worker financial health by increasing worker expenses. Gigworkers are responsible for all on-the-job expenses; for example, Uber drivers must pay for their
own gas and insurance. These costs may increase both the level and the volatility of workers’
expenses. For example, when gigs require the use of a worker’s personal resource (e.g. a car), gigs
may increase both the regular wear and tear on the resource and the likelihood of an unexpected
repair.
To determine the impact of gigs on the financial health of LMI workers, we first study the
effect of the launch of Uber’s UberX service on rates of financial hardship. UberX is the first
ride-sharing service offered by Uber that allows non-commercially licensed car owners to offer rides
for hire. Uber introduced this service in San Francisco in 2012, expanding the locations where
UberX is offered over time. Taking advantage of the geographic and temporal staggering of the
launch of UberX across locations, we estimate the causal effect of this launch on financial outcomes
via a difference-in-differences design, which controls for time-invariant geographic heterogeneity
as well as macroeconomic shocks experienced simultaneously across locations. Our work joins a
growing body of literature leveraging the sequential roll-out of gigs in this way (Burtch et al.,
2018; Greenwood and Wattal, 2017; Li et al., 2016b; Barrios et al., 2018; Zervas et al., 2017). Our
analysis shows that the entry of UberX leads to significantly higher rates of hardship among LMI
families. We test four possible mechanisms for this increase: long-run earnings, long-run expenses,
income volatility, and expense volatility. We find that, while UberX lowers income volatility, it also
decreases overall take-home pay (i.e. long-run earnings less long-run expenses) for LMI families.
We find no discernible effect on expense volatility. The net effect is diminished financial health for
LMI families.
The results of our difference-in-differences analysis demonstrate the effects of making gigs like
UberX available. These results are useful for policy makers who make interventions at the population level. We are also interested in measuring the impact of gigs at the individual level. Specifically, we would like to estimate the impact of gigs on the subpopulation that elects to participate
in gig-work. To do this, we leverage the reported ride-sharing behavior of survey participants.
We employ an instrumental variables approach to determine the effect of deciding to provide ridesharing services on the probability of experiencing a hardship. Our analysis estimates that LMI
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 individuals who ride-share are on average 27 percentage points more likely to experience hardship
than those that do not ride-share. Quantifying the substantial risk to LMI individuals who enter
the gig-economy should aid potential gig-workers evaluating the pros and cons of gig-work and
focus platforms’ attention on this potential threat to their supply base.
Our analysis makes two main contributions. First, we show that, despite the benefits of flexibility, gigs can be detrimental to the financial stability of their workers. We provide a plausible
estimate of the increase in risk of hardship resulting from working gigs, which can be used by workers weighing the costs and benefits of joining the gig-economy. Second, our analysis gives guidance
to regulators and platforms for how the financial health of gig workers might be preserved within
the gig-economy framework. We find that increased hardship is driven by decreased take-home pay,
not increased income volatility. Indeed, we find that gigs decrease income volatility. This suggests
that easy-to-implement interventions designed to boost per-service payments, like New York’s cap
on ride-share drivers, are more effective than efforts to reduce income volatility, like proposals to
impose a minimum hourly wage. These results highlight the possibility for well-designed gigs to
improve the financial health of LMI workers by allowing them to mitigate their income volatility.

2

Literature Review

There has been a wealth of recent interest in the operations of the gig economy. Most existing
work concerns the design of platform profit-maximizing matching (e.g. Feng et al. (2017); Ozkan
and Ward (2017); Hu and Zhou (2015)) and pricing (e.g. Cachon et al. (2017); Bimpikis et al.
(2016); Tang et al. (2016); Hu and Zhou (2017); Taylor (2018); Chen and Hu (2017); Guda and
Subramanian (2018)). Of particular relevance for this work are papers focusing on welfare implications of gig-economy platforms and their policies. Cachon et al. (2017) shows surge pricing can
benefit consumers by increasing supply availability. Castillo et al. (2017) shows that surge pricing
can destroy welfare by sending workers on wild goose chases during times of low demand. Afèche
et al. (2018) shows that increasing platform control improves worker welfare and platform profit.
Benjaafar et al. (2018) and Nikzad (2018) show that platform efforts to recruit ever more workers
do not necessarily destroy worker welfare by increasing competition but can also improve worker
welfare by attracting more consumers. Kalkanci et al. (2018) suggests that the gig economy has

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 the potential to increase economic inclusion by providing flexible income sources to low-income
populations. In this paper we demonstrate the extent to which this potential is realized.
The gig economy has inspired a number of empirical analyses (Kabra et al., 2018; Karacaoglu
et al., 2018; Li et al., 2016a). Many of these studies have focused on estimating supply elasticity
(e.g. Chen and Sheldon (2016); Cullen and Farronato (2014); Sheldon (2016); Hall et al. (2017)).
Others have compared Uber to conventional taxis, concluding that Uber better utilizes its drivers
(Cramer and Krueger, 2016) and that drivers benefit from Uber’s compensation scheme relative
to the weekly or daily leases common in the taxi industry (Angrist et al., 2017). Our analysis
estimates the causal impact of the launch of UberX in a location via a difference-in-differences
model. A similar approach has been used to study the effect of the entrance of a gig-economy
platform on entrepreneurship (Burtch et al., 2018), DUI citations (Greenwood and Wattal, 2017),
congestion (Li et al., 2016b), traffic fatalities (Barrios et al., 2018), and incumbent industry market
share (Kroft and Pope, 2014; Zervas et al., 2017).
The spread of gigs represents an increase in the availability of flexible work arrangements. In
general, contingent work arrangements have been shown to benefit firms by allowing them to only
pay for the workers they need (Kesavan et al., 2014; Milner and Pinker, 2001; Pinker and Larson,
2003). This translates to the ride-sharing setting via improved utilization of Uber drivers relative
to taxi drivers (Cramer and Krueger, 2016). Workers also stand to benefit from these flexible
work arrangements via the discretion allowed workers over their work schedules. Workers with this
discretion should be better able to integrate their work with other obligations (Chen and Sheldon,
2016). In particular, discretion should allow workers to supplement their income from day jobs
more easily (most Uber drivers hold another job (Hall and Krueger, 2015)). However, discretion
also allows workers to prioritize non-lucrative activities and is not always used to further a worker’s
career (Smithson et al., 2004).
Gigs also influence the volatility of worker income. The discretion associated with gigs should
allow workers to increase their time spent on gig-activities in response to an unexpected decrease in
outside income, thereby decreasing income volatility (Farrell and Greig, 2016). This is particularly
valuable for low-income families, who typically lack sufficient savings to weather downward shocks
to their income (Gunderson and Gruber, 2001; Bania and Leete, 2007). However, because gigs
pay per service instead of per hour, gigs also inherently increase per-hour income volatility. This
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 volatility is amplified by dynamic pricing policies, like Uber’s Surge Price, which pays workers more
per service during times of high demand. Our analysis contributes to the literature studying the
effect of income volatility on low-income workers by demonstrating the net effect of these competing
forces.
Our focus on worker financial hardship relates to the literature studying supply chain risk due
to supplier bankruptcy. Typical inventory-holding firms have a number of strategies for addressing
the threat of supplier default. For example, firms may engage in long term contracts (Swinney and
Netessine, 2009), subsidize unstable suppliers (Babich, 2010), or firms may engage in trade credit
(Kouvelis and Zhao, 2012). This threat has not been considered in traditional service settings where
service is supplied by obedient employees. In the gig-economy setting, the solvency of gig workers
can affect the supply of service - financially distressed workers may not be able to keep the car they
use to drive for Uber or the house they use to host Airbnb guests. While each individual worker’s
contribution to the platform’s service supply is small, systematic financial instability among workers
may affect worker retention, which may affect service quality (Pinker and Shumsky, 2000; Gans
et al., 2003) and which gig-economy platforms have identified as an area of concern (McGee, 2017).
Our work measures the extent to which supplier default is a concern within the gig-economy and
suggests targets for intervention by identifying antecedents for supplier insolvency.

3

Data and Descriptive Statistics

In our main analysis, we study the expansion of access to gigs via the launch of Uber’s UberX service,
which allows ordinary car owners (as opposed to licensed livery drivers) to drive for hire. Uber
introduced UberX in 2012 and continues to expand. Using launch announcements on Uber’s blog
(uber.com/blog) and in local news outlets, we collect the date of UberX launch for U.S. Metropolitan
Statistical Areas (MSAs). Figure 1 illustrates the roll-out of Uber’s UberX service across MSAs
over time. The sequential launch of UberX across locations lends itself to a difference-in-differences
design (Angrist and Pischke, 2008; Bertrand and Mullainathan, 2003). With this strategy, we
identify the effect of gaining access to UberX on outcomes related to individual financial health.
To construct our main dependent variables, we rely on two surveys. The first is the Household
Financial Survey (HFS), which documents survey responses of a random sample of taxpayers qual-

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 ifying for TurboTax’s Freedom Edition free tax filing package. To qualify for this “freefile” option,
a household must have an adjusted gross income no greater than $33,000 ($66,000 for active duty
military personnel) or must have received the earned income tax credit. This restriction allows us
to focus our analysis on LMI families, who we suspect will experience the greatest impact from
the introduction of UberX. Surveys were administered each year from 2013 to 2018 at the time
of tax filing, and the number of respondents varies from year to year. The survey asks questions
about financial behaviors, demographics, and location. Survey participants additionally consent
to share their anonymized tax returns. Table 1 provides summary statistics. Note that the HFS
skews younger, whiter, and better educated than the broader LMI population (see Figure 2), so
the magnitude of effects measured with the HFS population may not be directly extrapolated to
the broader LMI population. However, Figure 2 demonstrates that the HFS population is not so
niche that results derived from its study are unimportant. For example, if the results we detect
were confined to white, college-educated millennials, this demographic represents a sufficiently large
portion of the broader population that the results would still be relevant to decision-makers. Figure 2 also compares the HFS population with the demographics of Uber drivers reported in (Hall
and Krueger, 2015). The HFS is younger, whiter, and more female than the average Uber driver.
However, our analysis does not require every individual who gains access to UberX to become an
Uber driver. Instead, our results reflect the behavior of a subset of individuals who take advantage
of the opportunity created by UberX’s launch.
Our main dependent variable, hardship, measures financial hardship according to the binary
response to, “Was there a time in the past X months when you or someone in your household
skipped paying a bill or paid a bill late due to not having enough money?” (1 indicates yes). Note
that this question refers to the time interval beginning twelve months (i.e. X = 12) before the
survey in 2013 and 2014, while subsequent years refer only to the interval beginning six months
before the survey (i.e. X = 6). Though this leads to more reports of financial hardship in earlier
waves of the survey, the increase happens across the board (as opposed to only in locations with
UberX), so this difference across survey years is absorbed by the survey-year fixed effect included
in our analysis. Note that all other survey questions used to construct dependent variables in this
paper are consistently worded across relevant survey waves.
To explore the mechanisms through which UberX increases financial hardship, we study several
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 additional dependent variables from this survey. One mechanism we consider is income volatility.
Respondents are asked:
Which of the following best describes your household’s income over the last 6 months?
1. Roughly the same amount each month
2. Roughly the same most months, but some unusually high or low months
3. Often changes quite a bit from one month to the next
We classify respondents who select Choice 2 as experiencing moderate income volatility and respondents who select Choice 3 as experiencing severe income volatility. We also consider respondents
who report experiencing any income variability by selecting either Choice 2 or Choice 3. The associated dependent variables are mod vol, hi vol, and any vol respectively, where 1 indicates that a
respondent belongs to that category.
The hardship experienced by respondents may also be the result of unexpected expenses. We
consider three categories of unexpected expenses: car repairs, medical expenses, and legal expenses.
Driving for Uber causes additional wear and tear on a vehicle. When not properly prepared for,
this may lead to more frequent unexpected car repairs. Driving for Uber also increases the driver’s
exposure to vehicle collisions (Barrios et al., 2018), which may lead to medical and legal costs.
To measure the potential increase in these expense categories, we use respondents’ answers to the
following question:
In the last 6 months, have you or has any member of your tax household:
1. Made an unexpected major repair to a vehicle you own?
2. Had unexpected major out-of-pocket medical expense (e.g., from hospitalization or emergency
room visit)?
3. Had unexpected legal fees or legal expenses?
The binary variables, shock car, shock med and shock legal, take the value of 1 for respondents
who experienced an unexpected expense in each respective category. Note that questions interrogating respondent income volatility and unexpected expenses are only available for survey waves
2015-2017. Our analysis of these variables uses the corresponding subset of the HFS data.
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 Finally, we consider respondent gross income (captured by the variable gross income) as reported on the respondent’s anonymized tax return. We supplement this analysis by analyzing five
waves of the biennial Panel Survey of Income Dynamics (PSID) from 2007-2015. The PSID follows
families over time, recording granular information about household income and employment, along
with demographic and geographic information. We restrict our attention to the 3,835 households
with heads of household that are active in the survey during all of the years studied in this analysis
(the survey is primarily administered to heads of household). The PSID is a useful supplement to
the HFS for several reasons. First, the PSID breaks household income into its component parts
(i.e. income from labor, assets, transfers, etc), allowing us to focus on the component affected
by UberX entry: labor income. Further, the PSID includes detailed information about respondent work habits, allowing for more detailed explanations of the results of our analysis. Finally,
the panel structure of the PSID allows for controls of individual-specific idiosyncrasies. Table 2
provides descriptive statistics.
The PSID surveys families from all income brackets while the HFS surveys only those which
qualify to file their taxes for free. To ensure that our analysis of the PSID reflects outcomes of
the population studied in the HFS, we split the PSID data into two groups: those deemed “freefile
eligible” and those deemed “freefile ineligible.” Lacking information on household adjusted gross
income, we assign freefile eligibility based on total reported income. Specifically, families deemed
freefile eligible reported total income less than $33,000 in 2011, the last year surveyed before
Uber first introduced UberX. We designate freefile eligibility based on 2011 income to ensure that
group assignment is not influenced by treatment (our results are robust to alternative definitions
of freefile eligibility). Grouping households in this way allows us to identify outcomes specific to
LMI households.
Locations are considered treated if UberX has launched there by the end of the horizon considered by the survey. The HFS survey is administered when a respondent files his/her taxes. Lacking
information about the exact filing date, we assume survey questions refer to events through April
of the survey year. For example, a location is considered treated in survey year 2015 if UberX
launched there before April 1, 2015. We make an exception to this assumption when analyzing
gross income. Gross income reported on a tax return refers to income earned in the previous calendar year. Consequently, to affect gross income UberX would have to launch before the beginning
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 of the survey year. Similarly, PSID survey questions refer to quantities (e.g. income, work hours)
in the year preceding the survey year. For analysis of HFS income and PSID quantities, a location
is considered treated if UberX launches before January 1 of the survey year. The variable treatjt
indicates whether location j is treated in survey year t.
Finally, we include in our analysis controls for potential MSA-level heterogeneity. We obtain
estimates of population (pop) and the percent of the population with a college degree (%degree)
from the U.S. Census. We additionally include a measure of employment (emp) from the U.S.
Census Business Patterns series. This measures the number of non-government employees working
at organizations located within a MSA. In our analysis, we standardize this measure by dividing
by the MSA population (emp rate). Finally, we include a measure of income dispersion, the Gini
Index (gini), from the U.S. Census. This measure ranges from 0 to 1, with larger values indicating
greater inequality.

4

Analysis of Hardship

Our main analysis studies the effect of UberX entry on the likelihood a family experiences financial
hardship. Our dependent variable is hardship, which indicates whether a respondent failed to pay
a bill on time in the months preceding the survey (as defined in Section 3). Let i index individuals,
j index MSAs, and t index survey years. We estimate:
hardshipijt = αt + γj + βtreatjt + θ0 Xijt +  ijt

(1)

where αt is the survey year fixed effect that absorbs macroeconomics shocks felt across MSAs,
γj is the MSA fixed effect that captures the time-invariant attributes of a MSA, Xijt represents
individual characteristics, and treatjt is an binary variable indicating whether UberX has entered
MSA j before the survey in year t. We include as individual characteristics gender, race, education,
and marital status. These characteristics do not all vary with time, but they account for variation
in the demographic distribution of respondents representing a MSA across time. We further include as time-varying MSA characteristics population, percent of population with a college degree,
employment, and the Gini Index of income inequality. We exclude from our analysis MSAs that

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 UberX entered before the first survey wave (e.g. April, 2013) and MSAs that do not appear in
every survey wave. To ensure a non-trivial population of control MSAs (e.g. MSAs without UberX)
we exclude responses to the 2018 survey wave. UberX increases its market penetration each year,
and by 2018 just 0.05% of respondents hail from MSAs without UberX. This number is 6.3% in
2017 and 11.7% in 2016. For our main analysis, we employ surveys spanning April, 2013 to April,
2017, leaving 75,071 observations over 5 years with 49 untreated MSAs.
We report the results of our estimation in Table 3. Note that standard errors are adjusted
for clustering at the MSA level. We find that the launch of UberX corresponds to a significant
increase in financial hardship. In spite of the opportunities UberX offers families to improve their
financial security, UberX entry leads more LMI households to fail to meet their short-term financial
obligations. These results are robust to sample selection: Column 1 reports results using surveys
spanning 2013-2017 of data while Column 2 restricts analysis to data from 2013-2016. In Column
3, we generalize our specification to consider the evolution of this effect over time. Specifically, we
estimate
hardshipijt = αt + γj +

X

βk Tjtk + θ0 Xijt +  ijt

(2)

k

Tjtk is a relative time dummy variable. In this analysis we measure time in years to match the
annual nature of the HFS. Correspondingly, Tjtk represents whether UberX enters MSA j k years
from time t. Because Uber began offering UberX in 2012 and HFS survey responses span 2013-2017,
there are four possible leads and four possible lags. Estimation of Equation 2 illustrates that the
increase in hardship is sustained following UberX’s launch. Notably, our analysis does not detect
any pretreatment trends, indicating that, to the extent UberX launches are not random, they do
not target locations with increasing rates of hardship among LMI households. This lends credence
to the parallel trends assumption required to interpret these results causally.

5

Robustness

Our interpretation of the results in the previous section rests on several conditions. Causality
with the difference-in-differences specification requires that locations with and without UberX must
experience parallel trends in hardship during the years before UberX’s entry. Because Uber chooses
the locations to enter it is possible that Uber’s decision criteria correlate with hardship. To interpret
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 our results causally we must rule out this possibility. Additionally, the difference-in-differences
framework with staggered treatment exhibits serially correlated errors, as locations with high rates
of hardship in time t are likely to experience high rates of hardship in time t + 1. Our causal claim
requires our results to be driven by more than this serial correlation. The structure of our data
also introduces a challenge to causal interpretation. Because respondents are only drawn from LMI
families, it is possible that families who benefit from Uber are no longer present in the sample after
UberX entry. This truncation could lead to incorrect conclusions about the effect of UberX entry.
Finally, Model 1 assumes that the effect of UberX entry is constant across time and across MSAs.
In this section, we provide evidence that the conditions required for causal interpretation of our
result hold.

5.1

Parallel Trends

The parallel trends assumption is the key identifying assumption in any difference-in-differences
analysis. This demands particular attention in our setting where treatment is not exogenous.
In particular, because Uber decides where to launch, it is possible that Uber’s selection process
is correlated with financial hardship in candidate launch locations. This may be through direct
mechanisms (e.g. Uber prefers to launch in locations with high rates of hardship because people
experiencing hardship are likely Uber drivers) or indirect mechanisms (e.g. Uber prefers to launch
in populous locations, and people in populous areas are more likely to experience hardship).
To investigate the relationship between Uber’s location selection process, financial hardship, and
other observable characteristics of MSAs, we estimate a discrete-time (logit) hazard model (Singer
and Willett, 1993). In this model, the outcome of interest is a binary indicator of whether UberX
is available in an MSA at the time of the survey, measured for each MSA and for each survey year.
Observations following the launch are dropped from the analysis. We model the hazard of UberX
entry as a function of the proportion of respondents reporting hardship in an MSA, the logged MSA
population, the percent of MSA population with a college degree, the MSA’s proportion of nongovernment employees, and the MSA’s Gini index of inequality. Results are reported in Table 4. In
Column 1 we estimate a model that is a function of the level of predictor variables, and in Column
2 we estimate a model that is a function of the change in predictor variables (variable dif f ). Table
4 indicates a pattern to Uber’s entry decisions - Uber enters more populous, growing, and better
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 educated locations earlier. The model also indicates that Uber prefers locations with lower growth
in the population’s education, perhaps indicating a preference for markets with saturated high-skill
labor markets. Importantly, neither model indicates that Uber selects locations to enter directly
based on hardship. Hence, controlling for observable characteristics of candidate locations, as we
do in (1), alleviates concern about violations of the parallel trend assumption resulting from direct
selection on the outcome of interest.
We now turn our attention to the indirect mechanism. While Uber does not choose locations to
enter based on hardship, locations meeting Uber’s selection criteria may exhibit different trends in
hardship than locations that do not. To accommodate these potential differences, we extend Model
1 to include cohort-specific time trends. Specifically, we group MSAs into cohorts based on their
year of UberX entry (there are five cohorts, one for each year in the interval 2013-2017). MSAs in
the same cohort are similarly appealing to Uber as candidate locations. If our results are driven
by differential trends between more and less appealing-for-entry MSAs, then adding cohort-specific
trends will absorb these differences and produce insignificant estimates of the effect of UberX entry.
As shown in Table 3 Column 3, this analysis reduces our power but continues to demonstrate a
positive and marginally significant effect of UberX entry on hardship.

5.2

Random Implementation Test

The generalized difference-in-differences design is vulnerable to producing spurious results due to
the serial correlation in the errors of repeated observations (Bertrand et al., 2004). In all analyses,
we have clustered standard errors at the MSA level to address this concern. In this section, we
conduct two random implementation tests to ensure that our results are not a product of this serial
correlation (Greenwood and Agarwal, 2015).
Our goal is to test whether our results are distinguishable from placebo data, constructed such
that there is no inherently meaningful connection between the outcome (hardship) and treatment
(UberX entry). We consider two forms of placebo data. In the first, we swap the UberX entry
dates (or lack thereof) between locations. For example, Atlanta, GA may be assigned the entry
date of San Diego, CA (July, 2013), and San Diego may be assigned the entry date of St. Louis,
MO (September, 2015), and so on. In the second, we again swap the UberX entry dates between
locations, but in this test we only perform swaps between locations where UberX will eventually
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 launch (within the time frame of our data). For each set of randomly assigned entry dates, we
analyze the relationship between hardship and UberX according to the difference-in-differences
model in (1). We generate 1000 versions of each type of placebo data, yielding a distribution
of estimated placebo coefficients. We report the mean and standard deviation of the placebo
coefficients multiplying the treatment dummy in Table 5. We additionally compute the Z-score of
our original estimate of β from Table 3.
If the placebo coefficients from the first random implementation test resembled our original β,
this would indicate that serial correlation were a major concern. A resemblance between β and the
placebo coefficient in the second test would raise the possibility of serial correlation or of systematic
differences between the treated and control locations. Table 5 illustrates that for both random
implementation tests, the placebo coefficients are indistinguishable from zero. Furthermore, our
original estimate is significantly larger than the placebo coefficient. Taken together, this suggests
that our results are not driven by serial correlation and provides further evidence that there is no
significant, unobserved difference between locations with UberX and locations without.

5.3

HFS Truncation

It is interesting to focus on LMI households because (i) they are the most vulnerable to financial
hardship and (ii) they are more likely to participate in the gig-economy Smith (2016). However, the
exclusion of high income households from our primary data poses a challenge for our identification
strategy. To explain, consider an extreme hypothetical. Suppose that UberX positively impacts a
fraction of the population by reducing their hardship and increasing their incomes to at least the
freefile-eligibility threshold. Then following UberX entry, the HFS will not include any families
that experienced a positive effect from the UberX launch. Conclusions drawn from the remaining
population could be misleading. Similarly, if families negatively impacted by UberX appear in the
HFS data after UberX’s entry but not before, results comparing outcomes before and after may be
biased.
To address this potential bias, we examine our secondary data, the PSID. The PSID has two
advantages for addressing censorship of observations: (i) the PSID follows respondents from all
income brackets and (ii) the PSID is a panel of individuals (as opposed to the HFS’s repeated cross
sections). We use the first attribute to study the rate at which individuals move between freefile15
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 eligibility and -ineligibility across years (freefile eligible individuals report gross income less than
$33,000). Inspecting the data, the number of respondents leaving freefile-eligibility in the years
of UberX expansion (2013 -2015) is no greater than the number of respondents leaving freefileeligibility in the survey year prior to UberX’s initial roll-out (2011). Similarly, the number of
respondents joining the freefile-eligible group in the years of UberX expansion is no greater than
the number of respondents joining the freefile-eligible group the year prior to UberX’s initial roll-out
(See Table 6). To formalize this observation, we construct variables tracking whether an individual
becomes freefile-eligible (join) or becomes freefile-ineligible (leave). We use these measures as the
dependent variables in our difference-in-differences model and find no significant change in the flow
of individuals between income brackets resulting from UberX entry (see Table 7).
We use the panel structure of the PSID to categorize individuals’ freefile-eligibility before
UberX’s initial roll-out to study the effect of UberX’s launch on income of freefile-eligible and
-ineligible respondents. Table 10 Column 1 indicates that freefile-eligible respondents earn less
following UberX’s launch, while Column 2 shows that freefile-ineligible respondents earn more following UberX’s launch. This effect on income is opposite the effect that would drive the censoring
described above.

5.4

Heterogeneity of Effect over Time

Equation 1 assumes that the effect of treatment is constant for each year following UberX’s entry
and for each location UberX enters. While estimation of Equation 2 relaxes the constant nature of
the effect over time, it still suffers from the latter restriction. However, over time Uber has adjusted
its business model (e.g. driver commissions have shrunk) and awareness of Uber has grown on both
the demand and supply side. It is therefore plausible that the effect of UberX entry was different
for MSAs where UberX launched in 2013 than for MSAs where UberX launched in 2016. Here we
relax the assumption that the effect of UberX entry is the same for all entered MSAs. First, we
allow the effect of UberX entry to depend on the survey year. If the evolution of Uber’s business
model over time leads to decreasing payoffs to drivers, then more recent survey waves should exhibit
a larger increase in hardship than less recent survey waves. Second, we allow the effect of UberX to
vary by the year a MSA was entered. As in Section 5.1, we group MSAs into cohorts based on their
year of UberX entry. If the maturity of the UberX corresponds to increasing competition between
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 drivers, and hence lowers returns to drivers, then cohorts with earlier entry should experience a
more pronounced increase in hardship.
Table 8 reports our results. Column 1 reports significant increases in hardship from UberX
availability in survey years 2014 and 2017 (and a near significant effect in 2016). The magnitude of
the estimated effects do not demonstrate a systematic change in the effect size over time. Column 2
reports significant increases in hardship from UberX availability for cohorts receiving UberX access
between 2013 and 2015. The magnitude of the estimated effects do suggest that these cohorts
experience a greater increase in hardship than later cohorts. However, these cohorts represent
86% of the data, meaning our power to detect effects in the later cohorts is considerably less by
comparison. To the extent that we are willing to attribute this difference to market maturity (we
provide evidence that hardship trends do not differ across cohorts in Section 5.1), we should expect
those cohorts to demonstrate similar effects as estimated with other cohorts in the future.

6

Mechanisms

We now turn our attention to possible explanations for why we observe more hardship among
LMI families following UberX’s entry. To this end, we conceptualize hardship as a process that
evolves over time. Two important inputs to this process are (i) average monthly income and (ii)
average monthly expenses. Recall that a hardship occurs when short-term (e.g. monthly) bills
are not paid on time. If a family’s average monthly income does not exceed average monthly
expenses, the family will experience a hardship. However, this is not the only circumstance leading
to hardship. Many families experience deviations from their typical income and expenses. A family
with sufficient average income to cover average expenses but that experiences an unexpectedly large
expense or an unexpectedly small income one month may experience a hardship. See Figure 3 for
an illustration. From this process view of hardship, we identify four possible hardship antecedents
(i) steady-state income, (ii) steady-state expenses, (iii) income volatility, and (iv) expense volatility.
To study steady-state antecedents, we employ measures of annual income and expenses (average
monthly income = annual income/12). To study deviations from average income and expenses,
we rely on self-reported measures of income volatility and unexpected expenses. We focus on the
expense categories whose level and volatility Barrios et al. (2018) suggests may be affected by

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 UberX’s entry: vehicle operation and maintenance costs and medical expenses.

6.1

Annual Income

It is natural to expect that UberX’s entry could affect the take-home pay of the workers that choose
to drive for UberX. Ideally, we would measure this effect through gross income, which measures
all earnings less business expenses, including the costs of driving for Uber. As shown in Table
9, analysis of gross income reported in both data sets does not reveal any significant impact of
UberX entry for LMI households. Narrowing our attention to income earned from labor reveals
a significant impact of UberX entry. This measure is contained in the PSID and represents the
total annual income from wages, tips, commissions, overtime, professional practice as well as the
labor portion of any farm or business income earned by the head of household and spouse within a
family. Focusing specifically on labor income restricts attention to sources of income impacted by
UberX’s entry, reducing the noise in our estimation of UberX’s impact on income.
We adjust our analysis to leverage the panel structure of the PSID by introducing an individual
fixed effect, λi . The resulting model is:
labor incomeijt = αt + γj + λi + βtreatjt + θ0 Xijt +  ijt .

(3)

To match the biennial nature of the PSID, time in this model is measured in two-year increments.
The panel structure of the PSID removes the need for most individual level controls; those included
- number of children, martial status, age, educational attainment - vary with time. We additionally
include the time-varying MSA characteristics from our main analysis: population, percent of population with a college degree, employment, and the Gini Index of income inequality. We separately
analyze the effect of UberX entry on freefile-eligible and freefile-ineligible families.
Table 10 illustrates the relationship between UberX entry and labor income. Freefile-eligible
families report lower labor income in locations where UberX is available. This means that families
that would benefit the most from supplemental income earn less following UberX entry. In contrast,
freefile-ineligible families experience an increase in their labor income from UberX entry. Note that
these finding are robust to alternative definitions of freefile eligibility. Column 3 illustrates this
effect across federal head-of-household income brackets. Instead of splitting the data into freefile-

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 eligible and -ineligible, the model reported in Column 3 allows separate effects from UberX entry
for different income brackets. Brackets are defined as follows: bracket 1 = [0, $14,000), 2=[$14,000,
$52,000), 3=[$52,000,$84,000), 4=[$84,000,∞). Note that higher income brackets are collapsed into
bracket 4 to yield similarly sized populations in each bracket. Column 3 demonstrates that the
decrease in labor income is driven by households in the lowest bracket. For reference, an individual
working full time at the federal minimum wage earns $15,000 per year.
This result begs the question: why does income decrease among freefile-eligible households when
more employment options become available? While it is beyond the scope of this project to fully
account for all changes in work habits in response to gig-availability, we suggest that this result is
best understood in comparison to freefile-ineligible households. High-skill, high-wage workers have
much more access to work flexibility than low-skill, low-wage workers in traditional jobs (Bond and
Galinsky, 2011). It is natural, then, that these groups respond differently to access to a new form
of flexibility. In particular, low-income workers are willing to sacrifice some earnings for improved
control of their time while high-income workers have no need to make such a sacrifice. This choice
highlights the difference between worker welfare and worker financial health. This choice may
maximize worker utility. Unfortunately, it leaves workers at greater risk of exceeding their budget
constraint.
Note that this result suggests a possible endogenous UberX entry story. Specifically, UberX
may prefer to launch in locations with greater income inequality, artificially creating correlation in
entry with increasing income for the wealthy and decreasing income for the poor. For this reason
we have included the Gini Index of inequality in all of our analyses. Table 4 does not find a
relationship between UberX entry and income inequality, nor does including the Gini Index in our
difference-in-differences models absorb the effect of entry.

6.2

Annual Expenses

In addition to affecting the level of earnings families expect, UberX likely affects their expenses.
Barrios et al. (2018) suggests several expense categories that are likely to be relevant. The most
obvious expenses affected by UberX are transport costs. As independent contractors, Uber drivers
are responsible for expenses they incur on the job, including gasoline, for example. Second, Barrios
et al. (2018) shows that UberX entry leads to a greater volume of vehicle collisions, indicating that
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 drivers may be more likely to incur medical costs. As an additional expense category, we consider
child care costs. We include this expense category as an example of expenses that may decline as
a result of UberX: if the flexibility offered by Uber allows drivers to plan around the schedules of
their children, they may avoid paying for outside help.
Using the PSID, we construct the variables gasoline, medical, and childcare to capture the
annual dollars spent by a family on gasoline, out-of-pocket medical expenditures, and child care.
We substitute these dependent variables into Equation (3) to estimate the effect of UberX’s entry
on the level of these expenses. Table 11 reports the results. The only expense category that exhibits
a response to UberX entry is gasoline expenses. Though UberX does not drive higher child care
or medical costs, it does place the burden of Uber-related business expenses on drivers by design.
Taken together with the reduction in earnings reported in Section 5.1, this implies that UberX’s
launch reduces families’ net take home pay.

6.3

Income Volatility

To evaluate the effect of UberX’s launch on income volatility, we return to data provided by
the HFS. We study the likelihood that a family experiences moderate, severe, or any income
volatility. To do this, we re-estimate Equation (1) substituting mod vol, hi vol, and any vol as
our dependent variables. Note that these variables are available for survey waves 2015-2017, so we
exclude survey waves predating 2015 and MSAs with entry predating the 2015 survey wave, leaving
14,251 observations.
Table 12 demonstrates that the entry of UberX decreases reports of moderate (Column 1) and
any (Column 3) income volatility. Analyzing reports of severe income volatility does not reveal
any effect of UberX entry (Column 2), perhaps because relatively few (12%) respondents fall in
this category. These results are an interesting addition to the literature studying income volatility
and its effects in LMI populations. It is established that income volatility is dangerous for families
with few savings to draw upon if their regular income does not materialize. This might lead one to
conclude that the fee-per-service payment structure of gig work would be inherently damaging for
this population. However, gigs also provide a mechanism to counter income volatility. Specifically,
gigs allow workers to adjust their hours in response to earnings from either the platform or from
outside sources. Our findings demonstrate that this agency counteracts the extra income volatility
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 gigs might impose from their fee-per-service payment model.

6.4

Expense Volatility

The final potential drivers of hardship is expense volatility. It is possible that driving for Uber
introduces more frequent unexpected expenses, exhausting savings and leading families to fail to
pay their bills on time. We focus on expense categories whose volatility existing literature has
determined is likely to be affected by UberX’s entry: car repairs, medical expenses, and legal
expenses. Greater use of a driver’s vehicle may lead to more frequent component failures and
associated unexpected repairs. Further, as shown in Barrios et al. (2018), Uber’s launch increases
collisions, potentially exposing drivers to unexpected vehicle damages, medical costs, and legal fees.
Using the HFS data, we construct the variables shock car, shock med, and shock legal to
indicate whether a family experienced an unexpected expense in each category. We substitute
these measures as the dependent variable in Equation (1) to estimate the effect of UberX entry
on expense variability. These variables are only available for survey waves 2015-2017. The results,
reported in Table 13 indicate that UberX does not significantly increase expense volatility. This
suggests that, while Uber may cause more collisions, Uber drivers themselves may not be the
responsible party. We conclude that cost volatility is not a driving force behind the increased rates
of hardship reported in Section 4.
Taken in sum, our results indicate that the rise in hardship documented in Section 4 is attributable to the decline in net take home pay resulting from UberX’s entry. Reduced net income
leaves workers with a smaller buffer against unanticipated shocks. These shocks are fewer because
of UberX - we find that UberX reduces income shocks and has no significant effect on expense
shocks. However, the reduction in income volatility is insufficient to compensate for the reduction
in total income.

7

Effect on the Treated

Thus far, our results measure the effect of making gigs available. While we hypothesize that our
results are driven by respondents who work gigs when they are made available, it is possible that
our analysis detects spill-over effects. For example, it is possible that driving for Uber reduces

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 hardship among Uber drivers, but that the entry of Uber increases hardship among taxi drivers.
It is interesting to study the net effect of UberX entry within a population when considering
policies that increase or restrict a population’s access to gigs. However, we are also interested
in understanding the effect experienced by individuals that actually work gigs. In this section,
we provide a plausible estimate of the effect of driving for Uber on the likelihood of experiencing
hardship.
To do this, we employ respondents’ answers to the questions:
1. In the past year, did you earn any income through services offered through a mobile app or
website (sometimes known as the “Sharing” or “Gig” economy)?
2. Thinking about the income you earned through the mobile app or website, which of the
following best describes the work you do?”
• Ride-sharing/transportation services
• Home sharing services
• Making and selling products
• Shopping, delivery or warehouse services
• Performing tasks online (e.g. completing surveys or doing data entry)
• Performing household tasks like packing/moving, cleaning and laundry
These survey questions above were added to the to the HFS in 2017, so this information is less suited
to longitudinal analyses like difference-in-differences. Freed from the constraints of the differencein-differences framework, we include data from both 2017 and 2018 survey waves. Our goal is to
estimate the causal link between an individual’s decision to ride-share (rideshare) in a survey year
and the hardship experienced by the individual during the same survey year:

hardshipijt = f (ridesharei , Xij , αt , θ)

(4)

where Xij is the vector of individual i’s attributes and characteristics location j (individual i’s
location) from Equation 3, αt is a survey-year fixed effect, f () is a measurable real function, and

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 θ are parameters to be estimated. For computational ease, we take the log of MSA population for
this analysis.
As a first step, we employ a probit model to describe the relationship between hardship and ridesharing, i.e.f () = Φ(), the standard normal cumulative distribution. Column 1 of Table 14 reports
the average marginal effects of this model. This model reveals a positive and significant effect of
ride-sharing on hardship, estimating that, on average, ride-sharing corresponds to an increase in
the probability of hardship of 16.7 percentage points.
These results align with the positive effect of UberX entry on hardship reported in our main
analysis. However, ride-sharing is not exogenously assigned to respondents. Instead, respondents
may select to ride-share based on unobservable attributes correlated to hardship. For example,
respondents facing an impending hardship may attempt ride-sharing as a means to avoid that
hardship. To extract the causal impact of ride-sharing on hardship, we employ an instrumental
variable estimation approach developed by Abadie (2003).
A challenge of standard instrumental variable approaches in our setting (e.g. two-stage least
squares) is the binary nature of the endogenous variable, rideshare, and the outcome, hardship.
Consistent estimates require a linear models of the relationship between the endogenous variable
and the instrument and between the outcome and the endogenous variable. However, the constant
marginal effects of linear models can lead to nonsensical predictions when the outcome of interest
is binary.
In contrast, Abadie (2003)’s approach is tailored to binary endogenous variables and can accommodate binary outcomes. To explain the approach, let the binary endogenous variable represent
treatment into which respondents select. The goal is to estimate the parameters of the relationship
between outcome and treatment (e.g. θ) among respondents who are (endogenously) treated. The
challenge is that we do not observe the counterfactual outcome for treated respondents. Abadie
(2003)’s approach estimates θ by considering weighted outcomes for the entire population.
To construct the appropriate weights, a binary instrument is required. Like other instrumental
variable approaches, the instrument must be independent of the outcome conditioned on covariates, and the instrument must be correlated with the endogenous variable. Whether UberX has
entered a respondent’s location satisfies these requirements for our analysis. First, UberX entry is
a binary outcome. Second, UberX entry represents a significant increase in access to ride-sharing
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 opportunities, hence UberX entry is strongly related to a respondent’s decision to ride-share. We
estimate a probit model of the effect of UberX’s launch on respondent ride-sharing in Column 2
of Table 14 and find a positive, significant effect. Finally, we argue the our hazard model analysis
in Section 5.1 suggests that UberX entry is independent of hardship outcomes in a location after
controlling for observable characteristics of a location.
Weights are derived from the probability of experiencing the binary instrumental outcome. In
our analysis, we model this probability by a probit regression. We also assume the functional
relationship between hardship and ride-sharing may be modeled as a probit regression (i.e. f () =
Φ()). Column 3 of Table 14 reports the average marginal effect of ride-sharing on hardship to
be 21.0. This means, on average, choosing to ride-share increases the probability of hardship by
21 percentage points for members of LMI households. This result reveals that there is a positive
and significant effect of ride-sharing on hardship for LMI individuals who elect to ride-share. We
conclude that the results from our longitudinal analysis are not exclusively detecting spill-over
effects. Furthermore, this provides a plausible estimate of the effect of ride-sharing among those
that elect to participate. The substantial increase in hardship from ride-sharing indicates that
ride-sharing threatens the financial stability of LMI drivers in spite of the desirable flexibility that
ride-sharing offers.

8

Discussion

There is an open discussion about how to protect worker welfare in labor markets with independent
workers. On one hand, independent workers are empowered to adjust their work hours in response to
their needs, conceivably increasing income and averting hardship. However, workers that substitute
gigs for conventional work relinquish the security of traditional worker protections.
Our work is enabled by a novel data set that allows analysis not only of steady-state measures
of financial health but also of transient failures to meet financial responsibilities, which can have
snowballing effects for households living near their budget constraint. We show that, as currently
operated, UberX exacerbates financial hardship among low income families. Families in this population report greater difficulty meeting their financial obligations after UberX has launched in their
location. We attribute this increase in hardship to reduced net take-home pay - workers in locations

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 with UberX report earning less than their counterparts without access to UberX. Moreover, Uber
drivers are responsible for their on-the-job expenses, further reducing take-home pay. Financial
hardship is partially mitigated by reductions in income volatility following UberX’s launch, but
this is insufficient to fully compensate for workers’ lower pay.
There are three main contributions of this work. First, we caution that gigs can be exacerbate
financial instability among low income families. We estimate that the average LMI ride-share
driver experiences an increase in the probability of hardship equal to 21 percentage points. This
should inform workers considering taking up gigs: trading security for flexibility may lead to greater
financial hardship.
Second, our analysis of the mechanisms driving our main result illustrates why gigs increase
financial hardship among low-income households. We find that gig workers take home less pay
than non-gig workers, both because gig workers earn less and because gig workers bear the burden
of gig-related expenses. These results may serve as a guide to regulators and platforms interested
in maintaining worker financial health. Specifically, our findings suggest that easy-to-implement
interventions boosting expected gig-pay will go a long way toward improving financial outcomes
for gig-workers. The new cap on the number of ride-sharing vehicles allowed in New York City fits
this description.
However, our results may indicate that regulating the gig-economy may be a superficial solution to a deeper problem. Low-income households experience a different effect from gigs than
high-income households. In particular, low-income households earn less when they gain access to
gigs, while high-income households earn more. We suspect that this result is driven by access to
workplace flexibility (e.g. sick days and family leave). Low-skill, low-wage workers have little flexibility in their non-gig jobs and so may be willing substitute lower paying gigs for their inflexible
non-gig jobs to gain workplace flexibility, a substitution high-skill, high-wage workers need not
make. This may indicate that providing greater workplace flexibility in non-gig jobs would allow
workers to use gigs in ways that improve financial stability.
Finally, we demonstrate the effect of gigs on income volatility. While gigs may increase income
volatility by placing the burden of variable demand on workers, they may alternatively decrease
income volatility by empowering workers to dynamically adjust their work hours in response to
income shocks. This tension is inherent to the design of gigs - workers agree to bear the risk
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 associated with uncertain demand in exchange for autonomy over work hours. We find that this
trade is in the worker’s favor - gigs decrease income volatility. From a practical perspective, this
illustrates that addressing potential income volatility (e.g. via a minimum hourly wage) need not
be the focus of efforts to improve gig worker financial health. This result also reveals that, at a
fundamental level, gigs have the potential to improve the financial health of LMI workers, who are
more vulnerable to the adverse affects of income volatility.
Financial health is just one component of worker welfare. The fact that workers choose to work
gigs and experience a corresponding increase in hardship does not mean their choice is not utility
maximizing (Chen et al., 2017). By quantifying the financial impact of this choice, we hope to help
not just potential gig-workers but also gig-economy platforms concerned with worker retention and
regulators interested in constituent solvency evaluate the pros and cons of this work arrangement.

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9

Tables
Table 1: HFS Summary Statistics

hardship
treat
white
male
married
college
pop
%degree
emp
gini

mean

st.dev.

hardship

treat

white

male

married

college

pop

%degree

emp

gini

0.44
0.67
0.77
0.46
0.14
0.28
2, 238, 879
31.44
904, 060
0.46

0.50
0.47
0.42
0.50
0.34
0.45
2, 336, 577
7.00
973, 963
0.02

1
-0.13
-0.07
-0.12
0.06
-0.05
-0.03
-0.11
-0.04
-0.01

1
-0.02
0.05
-0.05
0.01
0.24
0.23
0.25
0.16

1
0.04
0.04
0.03
-0.12
-0.02
-0.11
-0.08

1
0.11
-0.04
0.01
0.02
0.01
-0.004

1
-0.004
-0.06
-0.08
-0.06
-0.04

1
0.01
0.02
0.01
-0.01

1
0.32
0.99
0.30

1
0.36
0.11

1
0.28

1

Table 2: PSID Summary Statistics

UberX access
tot inc
gas
kids
age h
married
high school degree
pop
emp
perc col degree
gini

MU

SD

UberX access

labor income

gas

kids

age h

married

high school degree

pop

emp

%degree

gini

0.18
59, 176
192
0.78
48.40
0.57
0.83
3, 505, 668
1, 403, 999
30.49
0.46

0.38
84, 125
193
1.16
14.79
0.50
0.37
4, 460, 305
1, 773, 229
6.59
0.02

1
0.03
-0.05
-0.04
0.13
-0.01
0.01
0.17
0.18
0.19
0.25

0.03
1
0.25
0.08
-0.08
0.35
0.18
0.12
0.12
0.12
0.03

-0.05
0.25
1
0.15
-0.07
0.34
0.12
-0.03
-0.04
-0.03
-0.01

-0.04
0.08
0.15
1
-0.40
0.19
-0.06
-0.05
-0.05
-0.05
-0.03

0.13
-0.08
-0.07
-0.40
1
0.05
-0.02
0.06
0.06
0.05
0.08

-0.01
0.35
0.34
0.19
0.05
1
0.09
-0.02
-0.02
-0.02
-0.06

0.01
0.18
0.12
-0.06
-0.02
0.09
1
0.03
0.03
0.10
-0.03

0.17
0.12
-0.03
-0.05
0.06
-0.02
0.03
1
1.00
0.37
0.53

0.18
0.12
-0.04
-0.05
0.06
-0.02
0.03
1.00
1
0.41
0.52

0.19
0.12
-0.03
-0.05
0.05
-0.02
0.10
0.37
0.41
1
0.16

0.25
0.03
-0.01
-0.03
0.08
-0.06
-0.03
0.53
0.52
0.16
1

31
Electronic copy available at: https://ssrn.com/abstract=3293988

 Figure 1: Number of MSAs with UberX Launches by Year1

1

Data current as of July, 2018

Figure 2: Comparison of HFS Population, LMI Population, and Uber Driver Population

Compares HFS population with the broader LMI population (defined as 200% of the federal
poverty line) and with attributes of Uber drivers as reported by Hall and Krueger (2015).

32
Electronic copy available at: https://ssrn.com/abstract=3293988

 Figure 3: Illustration of Hardship Process

Clockwise from upper left: (i) hardship from insufficient steady-state income to cover steady-state
expenses; (ii) no hardship when income = steady state income for each month, expenses = steady
state expenses for each month, and steady state income = steady state expenses; (iii) hardship
resulting from income volatility, despite sufficient steady state income; (iv) hardship resulting
from expense volatility, despite sufficient steady state income.

33
Electronic copy available at: https://ssrn.com/abstract=3293988

 Table 3: Difference in Differences Model of the Effect of UberX Entry on Hardship
Dependent variable:
hardship

treat

(1)

(2)

0.016∗∗

0.018∗∗

(0.007)

(0.008)

2 years after UberX entry
1 year after UberX entry
< 1 year after UberX entry
< 1 year before UberX entry
1 year before UberX entry

−0.176∗∗∗
(0.011)
0.031∗∗∗
(0.008)
0.168∗∗∗
(0.010)
−0.054∗∗∗
(0.007)
−0.094∗∗∗
(0.004)
−0.022
(0.022)
−0.033∗∗∗
(0.008)
0.089∗∗∗
(0.013)
−0.167∗∗∗
(0.006)
−0.225∗∗∗
(0.014)
0.073∗∗∗
(0.010)
0.097∗∗∗
(0.007)
0.081∗∗∗
(0.004)
−0.060∗∗∗
(0.008)
−0.062∗∗∗
(0.007)
−0.00000
(0.00000)
0.003
(0.004)
−0.742∗∗
(0.352)
−0.094
(0.233)

−0.170∗∗∗
(0.011)
0.035∗∗∗
(0.008)
0.170∗∗∗
(0.010)
−0.051∗∗∗
(0.008)
−0.096∗∗∗
(0.005)
−0.037
(0.031)
−0.029∗∗∗
(0.009)
0.093∗∗∗
(0.015)
−0.167∗∗∗
(0.007)
−0.203∗∗∗
(0.016)
0.081∗∗∗
(0.011)
0.107∗∗∗
(0.009)
0.085∗∗∗
(0.005)
−0.063∗∗∗
(0.010)
−0.068∗∗∗
(0.008)
−0.00000
(0.00000)
0.006
(0.005)
−0.439
(0.471)
0.208
(0.291)

Y
Y
N

Y
Y
N

Y
Y
N

Y
Y
Y

75,071
0.112
0.108
0.468 (df = 74745)

52,136
0.116
0.111
0.470 (df = 51811)

75,071
0.112
0.108
0.468 (df = 74739)

75,071
0.112
0.108
0.468 (df = 74738)

≥ 3 years before UberX entry

black
white
male
other gender
married
separated
single, never married
widowed
some high school
high school diploma
some college
some grad/professional school
Grad/professional degree
pop
%degree
emp rate
gini
Survey Year Fixed Effects
MSA Fixed Effects
Cohort Specific Time Trends
Observations
R2
Adjusted R2
Residual Std. Error

0.013∗
(0.008)

0.002
(0.009)
−0.021
(0.014)
−0.030
(0.020)
−0.175∗∗∗
(0.011)
0.031∗∗∗
(0.008)
0.168∗∗∗
(0.010)
−0.054∗∗∗
(0.007)
−0.094∗∗∗
(0.004)
−0.022
(0.022)
−0.033∗∗∗
(0.008)
0.089∗∗∗
(0.013)
−0.167∗∗∗
(0.006)
−0.225∗∗∗
(0.014)
0.073∗∗∗
(0.010)
0.097∗∗∗
(0.007)
0.081∗∗∗
(0.004)
−0.060∗∗∗
(0.008)
−0.062∗∗∗
(0.007)
−0.00000
(0.00000)
0.003
(0.004)
−0.705∗∗
(0.351)
−0.110
(0.234)

2 years before UberX entry

hispanic

(4)

0.039∗∗
(0.018)
0.028∗∗
(0.013)
0.025∗∗
(0.010)
0.023∗∗∗
(0.008)
Omitted

≥ 3 years after UberX entry

asian

(3)

−0.176∗∗∗
(0.011)
0.031∗∗∗
(0.008)
0.168∗∗∗
(0.010)
−0.054∗∗∗
(0.007)
−0.094∗∗∗
(0.004)
−0.022
(0.022)
−0.033∗∗∗
(0.008)
0.089∗∗∗
(0.013)
−0.167∗∗∗
(0.006)
−0.225∗∗∗
(0.014)
0.073∗∗∗
(0.010)
0.097∗∗∗
(0.007)
0.081∗∗∗
(0.004)
−0.060∗∗∗
(0.008)
−0.063∗∗∗
(0.007)
−0.00000
(0.00000)
0.002
(0.004)
−0.794∗∗
(0.361)
−0.093
(0.234)

∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

Note:

34
Electronic copy available at: https://ssrn.com/abstract=3293988

 Table 4: Hazard Model of UberX Entry
Dependent variable:
treat
(1)
hardship
pop
%degree
emp rate
gini

(2)

−0.264
(0.655)
.000001∗∗∗
(0.00000)
0.058∗∗∗
(0.013)
−1.783
(1.287)
1.852
(3.295)

hardship diff

0.338
(0.414)
0.0001∗∗∗
(0.00002)
−0.359∗∗
(0.177)
8.004
(12.459)
−4.438
(4.183)

pop diff
%degree diff
emp rate diff
gini diff
Survey Year Fixed Effects

Y

Y

Observations
Log Likelihood
Akaike Inf. Crit.

1,148
−410.616
841.231

837
−407.479
832.958

Note:

∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

35
Electronic copy available at: https://ssrn.com/abstract=3293988

 Table 5: Random Implementation Test

Estimates
µ
σ
Estimated Value
Z-score
p-value
Replications

Random Entry Date

Entry Date Swap Between Treated

β

β

0.0001
0.007
0.016
2.27
p = .011
1000

0.004
0.006
0.016
2.00
p = .022
1000

Notes: This table reports the average (µ) and standard deviation (σ) of the lag coefficients estimated from
placebo data generated by assigning UberX entry dates randomly. The p-values show that probability that
the simulated averages are as large as the estimated values in Table 3 is small.

Table 6: Number of Respondents Moving between Freefile-Eligibility and Freefile-Ineligibility in
the PSID

Transfers from freefile-ineligible
Transfers from freefile-eligible

2008

2010

2012

2014

225
303

320
175

229
215

215
201

Notes: The table provides counts of the number of PSID respondents whose income dropped below the
freefile-eligibility threshold after being freefile-ineligible during the prior survey (transfers from freefileineligible) and the number of PSID respondents whose income rose above the freefile-eligibility threshold
after being freefile-eligible during the prior survey for each survey year. The total number of PSID respondents is 3826.

36
Electronic copy available at: https://ssrn.com/abstract=3293988

 Table 7: Differences in Differences Model of the Effect of UberX Entry on Freefile Eligibility
Dependent variable:

treat
Survey Year Fixed Effects
MSA Fixed Fixed Effects
Individual Fixed Effects
Time-varying MSA and Individual Attributes
Observations
R2
Adjusted R2
Residual Std. Error (df = 14930)

join

leave

(1)
0.008
(0.013)

(2)
-0.009
(0.005)

Y
Y
Y
Y

Y
Y
Y
Y

19,042
0.214
- 0.002
0.221

19,042
0.233
0.022
0.207

Notes: Dependent variables indicate whether an individual became freefile eligible (join) or became freefile
ineligible (leave). Individual attributes include marital status, age, number of children, and grades completed. MSA attributes include population, employment, and education for all columns. Standard errors are
clustered at the MSA level. ∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

37
Electronic copy available at: https://ssrn.com/abstract=3293988

 Table 8: Heterogeneous Effects of UberX Entry
Dependent variable:
hardship
(1)

(2)

0.027∗∗
(0.011)
0.004
(0.009)
0.021
(0.013)
0.032∗∗
(0.013)

2014 survey year treatment effect
2015 survey year treatment effect
2016 survey year treatment effect
2017 survey year treatment effect

−0.175∗∗∗
(0.011)
0.031∗∗∗
(0.008)
0.168∗∗∗
(0.010)
−0.054∗∗∗
(0.007)
−0.094∗∗∗
(0.004)
−0.022
(0.022)
−0.033∗∗∗
(0.008)
0.089∗∗∗
(0.013)
−0.167∗∗∗
(0.006)
−0.225∗∗∗
(0.014)
0.073∗∗∗
(0.010)
0.097∗∗∗
(0.007)
0.081∗∗∗
(0.004)
−0.060∗∗∗
(0.008)
−0.062∗∗∗
(0.007)
−0.00000
(0.00000)
0.003
(0.004)
−0.726∗∗
(0.353)
−0.096
(0.232)

0.022∗
(0.012)
0.016∗
(0.009)
0.023∗∗
(0.010)
0.003
(0.017)
−0.002
(0.026)
−0.176∗∗∗
(0.011)
0.031∗∗∗
(0.008)
0.168∗∗∗
(0.010)
−0.054∗∗∗
(0.007)
−0.094∗∗∗
(0.004)
−0.022
(0.022)
−0.033∗∗∗
(0.008)
0.089∗∗∗
(0.013)
−0.167∗∗∗
(0.006)
−0.225∗∗∗
(0.014)
0.073∗∗∗
(0.010)
0.097∗∗∗
(0.007)
0.081∗∗∗
(0.004)
−0.060∗∗∗
(0.008)
−0.062∗∗∗
(0.007)
−0.00000
(0.00000)
0.002
(0.004)
−0.810∗∗
(0.356)
−0.088
(0.232)

Y
Y

Y
Y

75,071
0.112
0.108
0.468 (df = 74742)

75,071
0.112
0.108
0.468 (df = 74741)

2013 cohort treatment effect
2014 cohort treatment effect
2015 cohort treatment effect
2016 cohort treatment effect
2017 cohort treatment effect
asian
hispanic
black
white
male
other gender
married
separated
single, never married
widowed
some high school
high school diploma
some college
some grad/professional school
grad/professional degree
pop
%degree
emp rate
gini
Survey Year Fixed Effect
MSA Fixed Effect
Observations
R2
Adjusted R2
Residual Std. Error

∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

Note:

38
Electronic copy available at: https://ssrn.com/abstract=3293988

 Table 9: Difference in Difference Model of the Effect of UberX Entry on Gross Income
Dependent variable:inc gross

treat
Survey Year Fixed Effects
MSA Fixed Effects
Individual Fixed Effects
Time Varying Individual and MSA Attributes
Observations
R2
Adjusted R2
Residual Std. Error

HFS

PSID: freefile-eligible

PSID: freefile-ineligible

163.157
(151.738)

-1,472.269
(2,527.200)

11,280.130∗
(6,317.072)

Y
Y
N
Y

Y
Y
Y
Y

Y
Y
Y
Y

65,485
0.142
0.137
9,783.297 (df = 65157)

7,995
0.492
0.342
24,745.080 (df = 6166)

11,117
0.538
0.405
134,880.200 (df = 8623)

∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

Note:

39
Electronic copy available at: https://ssrn.com/abstract=3293988

 Table 10: Difference in Differences Model of the Effect of UberX Entry on Labor Income
Dependent variable:
labor income

treat

Freefile-Eligible

Freefile-Ineligible

−1,746.033∗
(1,057.104)

4,861.972∗
(2,534.550)

All

203.989
(403.845)
720.013
(734.769)
−6,546.448
(4,992.388)
842.454
(2,545.606)
−5,814.909
(5,735.466)
−9,901.747∗
(5,956.753)
1,566.791
(4,761.356)
−3,800.812
(4,331.862)
−2,788.077
(4,819.701)
−2,279.671
(4,695.852)
−3,419.347
(3,892.831)
−3,178.316
(3,691.510)
−1,719.296
(3,824.664)
−610.668
(3,774.676)
2,478.922
(3,817.186)
3,198.337
(3,885.475)
2,753.104
(4,595.643)
1,664.719
(4,785.110)
7,106.177
(4,839.008)
2,073.817
(4,248.634)
−15,105.280∗∗∗
(2,006.186)
−8,032.235∗∗∗
(2,881.842)
−13,247.040∗∗∗
(2,543.930)
−11,441.800∗∗∗
(2,289.817)
0.003∗∗
(0.001)
6,347.579
(18,580.550)
−133.405
(554.285)
−85,934.240∗∗∗
(30,730.870)

1,662.218
(1,147.944)
2,136.852
(1,477.741)
−49,893.280
(47,157.690)
41,188.180
(35,563.410)
24,142.740∗∗∗
(7,786.381)
45,552.940
(34,637.540)
5,367.323
(7,132.261)
20,359.040
(16,027.840)
38,854.870∗∗
(18,312.490)
36,468.890∗∗
(17,398.100)
28,617.390∗
(17,364.540)
30,597.410∗
(16,716.670)
29,257.510∗
(16,388.210)
28,823.870∗
(17,340.010)
25,486.580
(17,645.050)
30,270.290∗
(17,663.360)
28,680.990
(18,229.480)
36,221.970∗∗
(17,177.000)
40,380.680∗∗
(17,784.810)
27,142.380
(16,969.010)
−45,906.670∗∗∗
(5,869.412)
−21,630.800∗∗
(10,277.770)
−29,898.870∗∗∗
(4,473.359)
−28,272.090∗∗∗
(6,543.613)
0.003
(0.003)
20,193.870
(38,308.430)
943.552
(1,260.660)
−45,484.310
(46,343.540)

-2,472.433∗∗
(1,242.479)
337.508
(1,370.848)
4493.084∗
(2,476.353)
7,104.848∗∗
(2,840.791)
1,423.589∗∗
(665.407)
1,966.813∗∗
(897.018)
-25,610.110
(25,431.890)
611.333
(4,573.843)
7,268.638∗
(4,213.849)
9,674.701
(10,071.970)
7,337.832
(6,239.405)
8,187.300
(5,818.827)
15,116.610∗∗
(6,913.451)
12,302.140∗∗
(5,920.298)
9,072.688∗
(4,899.431)
9,314.975∗∗
(4,585.761)
9,426.124∗∗
(4,582.459)
9,660.216∗
(4939.148)
9,043.881∗
(5212.835)
12,827.470∗∗
(5,185.679)
13,049.080∗∗
(5,675.217)
21,411.310∗∗∗
(5,824.333)
25,762.640∗∗∗
(5,692.816)
11,020.500∗∗
(5,080.072)
-33,539.420∗∗∗
(4,070.339)
-16,709.060∗∗∗
(3,660.665 )
-25,945.000∗∗∗
(3,170.934)
-22,652.020∗∗∗
(3,272.754)
0.005∗∗
(0.002)
15,134.050
(22,709.790)
654.308
(762.279)
-58,379.680∗∗∗
(28,490.210)

8,015
0.637
0.530
15,375.970 (df = 6186)

11,155
0.767
0.700
52,840.880 (df = 8661)

19,090
0.802
0.747
42,053.960 (df=14983)

treat:bracket 1
treat:bracket 2
treat:bracket 3
treat:bracket 4
kids
age
grades completed: 1
grades completed: 2
grades completed: 3
grades completed: 4
grades completed: 5
grades completed: 6
grades completed: 7
grades completed: 8
grades completed: 9
grades completed: 10
grades completed: 11
grades completed: 12
grades completed: 13
grades completed: 14
grades completed: 15
grades completed: 16
grades completed: 17 or higher
grades completed: unknown
never married
widowed
divorced or annulled
separated
pop
emp rate
%degree
gini
Observations
R2
Adjusted R2
Residual Std. Error

∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

Note:

40
Electronic copy available at: https://ssrn.com/abstract=3293988

 41

Electronic copy available at: https://ssrn.com/abstract=3293988

Note:

Observations
R2
Adjusted R2
Residual Std. Error

gini

%degree

emp rate

pop

separated

divorced or annulled

widowed

never married

grades completed: unknown

grades completed: 17 or more

grades completed: 16

grades completed: 15

grades completed: 14

grades completed: 13

grades completed: 12

grades completed: 11

grades completed: 10

grades completed: 9

grades completed: 8

grades completed: 7

grades completed: 6

grades completed: 5

grades completed: 4

grades completed: 3

grades completed: 2

grades completed: 1

age

kids

treat

7,970
0.411
0.236
492.355 (df = 6141)

12.460
(32.578)
89.569∗∗∗
(28.603)
22.030
(28.694)
9.957
(55.855)
82.515
(77.118)
92.704
(132.745)
64.081
(88.101)
59.665
(86.177)
43.077
(96.736)
19.753
(92.516)
47.848
(121.484)
50.332
(112.048)
−9.602
(88.693)
38.824
(83.971)
−42.404
(88.845)
−35.293
(105.564)
38.488
(101.078)
1.096
(96.381)
68.005
(137.223)
353.264
(226.834)
−18.236
(86.106)
−29.070
(50.594)
74.517
(54.120)
61.043
(161.878)
155.994
(114.870)
0.00004
(0.00004)
802.449∗∗
(362.391)
−17.897
(13.646)
−1,006.285
(822.405)

Freefile-Eligible

11,112
0.588
0.469
1,949.122 (df = 8618)

46.505
(87.113)
677.056∗∗∗
(95.242)
−17.863
(102.461)
1,131.227
(766.207)
−1,151.869∗∗∗
(412.933)
−1,316.314∗∗∗
(319.823)
−205.062
(387.955)
241.588
(171.665)
−134.841
(309.552)
−40.134
(431.713)
−634.585
(516.699)
−391.260
(425.717)
−224.034
(397.143)
−564.998
(351.921)
−358.363
(391.013)
−440.313
(408.146)
−356.089
(415.282)
−384.519
(579.661)
−291.877
(412.762)
−107.112
(428.213)
−246.834
(396.110)
−441.574
(385.471)
422.928∗
(234.315)
−413.773∗
(243.532)
−239.971
(215.119)
0.0002∗∗
(0.0001)
1,474.282
(1,855.783)
29.057
(56.101)
−541.979
(2,338.496)

Freefile-Ineligible

childcare

10,783
0.362
0.170
2,701.169 (df = 8290)

110.671
(162.663)
48.237
(143.035)
17.109
(65.695)
−1,146.659
(729.727)
−566.661
(486.276)
−514.982
(473.943)
−366.545
(481.445)
−190.047
(535.884)
−440.046
(677.190)
−2,661.700∗∗
(1,272.450)
−822.055∗∗
(387.848)
−397.146
(432.473)
−775.883∗
(450.468)
−676.726∗∗
(342.566)
−903.646∗∗∗
(307.776)
−881.751∗∗∗
(326.619)
−856.752∗∗
(385.826)
−763.862∗∗
(345.013)
−1,174.298∗∗∗
(347.510)
−1,320.850∗∗∗
(428.804)
−1,147.627∗∗∗
(301.917)
−379.490∗∗
(168.278)
−168.747
(820.472)
−406.725∗∗
(188.691)
−135.346
(221.944)
−0.00001
(0.0002)
643.443
(2,020.167)
−8.616
(84.686)
3,036.346
(2,684.234)

−148.819
(117.118)
−1.349
(24.155)
204.709
(139.654)
1,302.721
(1,360.712)
6.020
(272.362)
−341.587
(528.738)
93.368
(548.974)
−261.365
(649.140)
194.547
(390.010)
1,178.478
(1,685.051)
−319.506
(481.532)
175.286
(425.471)
−1.544
(432.283)
−107.364
(447.368)
−245.661
(519.756)
−27.826
(492.978)
−92.896
(502.915)
93.008
(507.216)
51.398
(533.543)
172.914
(613.643)
−139.816
(409.434)
−291.853∗∗
(133.645)
−295.142
(243.949)
−210.405
(251.514)
−207.348
(155.838)
0.00005
(0.0001)
5,076.936∗∗∗
(1,861.358)
−6.660
(40.355)
−482.650
(2,463.284)
7,752
0.379
0.188
1,617.649 (df = 5924)

Freefile-Ineligible

Freefile-Eligible

medical

Dependent variable:

∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

10,996
0.522
0.382
159.283 (df = 8502)

20.183∗∗
(9.593)
9.849∗∗∗
(3.395)
3.745
(5.746)
119.372∗∗∗
(32.052)
−77.808
(62.814)
97.487∗∗∗
(26.780)
72.690
(63.820)
57.250∗∗∗
(15.767)
93.741∗
(50.115)
161.048∗∗
(66.704)
149.583∗∗
(58.857)
128.097∗∗
(59.858)
165.852∗∗∗
(56.373)
150.886∗∗∗
(49.697)
147.555∗∗∗
(48.730)
151.974∗∗∗
(50.253)
135.481∗∗∗
(49.336)
139.119∗∗∗
(49.747)
134.861∗∗∗
(48.650)
148.166∗∗∗
(49.655)
124.792∗∗∗
(48.191)
−45.125∗∗∗
(17.365)
−24.733
(35.130)
−86.519∗∗∗
(19.288)
−96.722∗∗∗
(17.796)
−0.00001
(0.00001)
−49.033
(165.781)
−5.391
(4.902)
175.669
(300.282)

Freefile-Ineligible

gasoline

7,833
0.563
0.431
115.071 (df = 6005)

7.333
(6.750)
4.891
(3.392)
16.697∗∗∗
(5.967)
−10.826
(18.449)
−39.763∗∗
(16.906)
25.221
(49.098)
−6.007
(34.618)
−0.142
(45.529)
−39.598
(52.584)
5.937
(48.960)
−8.697
(32.551)
2.357
(35.583)
7.923
(28.279)
6.524
(26.485)
−4.257
(29.898)
13.778
(35.908)
18.228
(34.638)
−0.822
(34.776)
−16.219
(35.279)
−2.756
(32.340)
30.598
(34.234)
−50.223∗∗∗
(16.792)
−28.498
(18.499)
−53.322∗∗∗
(13.881)
−34.788∗∗
(16.781)
−0.00001
(0.00001)
−101.128
(108.887)
−1.575
(2.303)
−133.032
(208.467)

Freefile-Eligible

Table 11: Difference in Differences Model of the Effect of UberX Entry on Expenses

 Table 12: Difference in Differences Models of the Effect of UberX Entry on Income Volatility
Dependent variable:

treat
asian
hispanic
black
white
male
other gender
married
separated
single, never married
widowed
grad/professional degree
high school diploma
some college
some grad/professional school
some high school
pop
%degree
emp rate
gini

modincvol

hiincvol

anyincvol

(1)

(2)

(3)

−0.039∗∗
(0.017)
0.079∗∗∗
(0.018)
−0.022
(0.025)
−0.023
(0.020)
0.029
(0.019)
0.018∗∗
(0.009)
−0.156∗∗∗
(0.042)
−0.028∗
(0.016)
−0.034
(0.028)
−0.026∗∗
(0.013)
0.190∗∗∗
(0.024)
0.026
(0.017)
−0.019∗
(0.012)
−0.040∗∗∗
(0.011)
−0.006
(0.020)
−0.054∗∗
(0.025)
−0.000
(0.00000)
−0.022
(0.018)
0.841
(0.866)
0.453
(0.434)

0.006
(0.010)
−0.041∗∗∗
(0.013)
0.018
(0.016)
0.015
(0.015)
−0.015
(0.014)
0.002
(0.005)
0.043
(0.036)
−0.018∗
(0.011)
0.044∗
(0.025)
0.001
(0.008)
−0.077∗∗∗
(0.013)
0.002
(0.011)
0.012
(0.009)
0.012
(0.008)
0.001
(0.012)
0.036∗∗
(0.017)
−0.00000
(0.00000)
0.012
(0.011)
0.065
(0.749)
−0.247
(0.289)

−0.032∗
(0.017)
0.037∗∗
(0.019)
−0.005
(0.020)
−0.008
(0.018)
0.013
(0.015)
0.020∗∗∗
(0.007)
−0.113∗∗∗
(0.032)
−0.047∗∗∗
(0.012)
0.011
(0.023)
−0.026∗∗
(0.011)
0.114∗∗∗
(0.020)
0.028∗∗
(0.013)
−0.007
(0.013)
−0.028∗∗∗
(0.010)
−0.005
(0.014)
−0.018
(0.023)
−0.00000
(0.00000)
−0.010
(0.017)
0.905
(0.869)
0.206
(0.423)

Y
Y

Y
Y

Y
Y

14,268
0.027
0.015
0.476

14,268
0.016
0.004
0.328

14,268
0.019
0.007
0.423

Survey Year Fixed Effects
MSA Fixed Effects
Observations
R2
Adjusted R2
Residual Std. Error (df = 14094)

∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

Note:

42
Electronic copy available at: https://ssrn.com/abstract=3293988

 Table 13: Difference in Difference Model of the Effect of UberX Entry on Unexpected Expenses
Dependent variable:

treat
asian
hispanic
black
white
male
other gender
married
separated
single, never married
widowed
grad/professional degree
high school diploma
some college
some grad/professional school
some high school
pop
%degree
emp rate
gini
Survey Year Fixed Effects
MSA Fixed Effects
Observations
R2
Adjusted R2
Residual Std. Error

shock car

shock med

shock legal

(1)

(2)

(3)

−0.013
(0.017)
−0.097∗∗∗
(0.028)
−0.018
(0.019)
−0.023
(0.024)
−0.021
(0.023)
−0.009
(0.007)
0.039
(0.038)
0.054∗∗∗
(0.020)
0.054
(0.036)
−0.064∗∗∗
(0.013)
−0.101∗∗∗
(0.026)
0.008
(0.018)
−0.019
(0.014)
0.014
(0.009)
0.016
(0.017)
−0.024
(0.027)
0.00000
(0.00000)
−0.020
(0.017)
1.032
(0.864)
−0.215
(0.364)

−0.009
(0.013)
0.007
(0.018)
0.038∗∗∗
(0.014)
0.031
(0.019)
0.030∗∗
(0.014)
−0.019∗∗∗
(0.006)
0.037
(0.031)
0.011
(0.015)
0.015
(0.029)
−0.074∗∗∗
(0.011)
−0.018
(0.022)
−0.018
(0.013)
0.022∗
(0.011)
0.021∗∗∗
(0.008)
0.014
(0.013)
0.017
(0.021)
−0.00000
(0.00000)
0.012
(0.014)
1.524∗
(0.798)
0.093
(0.308)

−0.008
(0.009)
−0.030∗∗
(0.013)
0.023∗∗
(0.010)
0.033∗∗
(0.013)
−0.001
(0.010)
0.007
(0.004)
0.022
(0.022)
−0.044∗∗∗
(0.010)
0.063∗∗∗
(0.023)
−0.055∗∗∗
(0.009)
−0.046∗∗∗
(0.015)
0.005
(0.008)
0.018∗∗∗
(0.007)
0.028∗∗∗
(0.006)
0.004
(0.008)
0.054∗∗∗
(0.015)
−0.00000
(0.00000)
−0.011
(0.008)
0.975∗
(0.560)
0.189
(0.217)

Y
Y

Y
Y

Y
Y

14,251
0.025
0.013
0.471 (df = 14077)

14,251
0.035
0.023
0.375 (df = 14077)

14,250
0.027
0.015
0.265 (df = 14076)

∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

Note:

43
Electronic copy available at: https://ssrn.com/abstract=3293988

 Table 14: Average Marginal Effect of Ride-Sharing
Dependent variable:
hardship

rideshare

hardship

(1)

(2)

(3)

0.167∗∗∗

rideshare

0.210∗∗∗
(0.078)

(0.023)

−0.033∗∗
(0.014)
−0.201∗∗∗
(0.009)
0.141∗∗∗
(0.013)
0.097∗∗∗
(0.033)
−0.077∗∗∗
(0.009)
−0.037∗
(0.022)
−0.093∗∗∗
(0.005)
0.003
(0.021)
−0.024∗∗
(0.010)
0.106∗∗∗
(0.022)
−0.161∗∗∗
(0.008)
−0.190∗∗∗
(0.011)
0.056∗∗∗
(0.016)
0.072∗∗∗
(0.009)
0.067∗∗∗
(0.006)
−0.066∗∗∗
(0.009)
−0.059∗∗∗
(0.009)
−0.005∗∗
(0.002)
−0.005∗∗∗
(0.000)
0.229∗∗∗
(0.047)
0.292∗∗
(0.116)
0.066
(0.053)

0.012∗∗∗
(0.001)
−0.004∗
(0.002)
−0.004∗
(0.002)
0.011∗∗∗
(0.004)
−0.001
(0.006)
−0.005∗∗
(0.002)
−0.002
(0.004)
0.010∗∗∗
(0.001)
0.003
(0.006)
−0.002
(0.002)
−0.002
(0.004)
−0.002
(0.002)
−0.006∗∗
(0.003)
−0.009∗∗∗
(0.001)
−0.006∗∗∗
(0.001)
−0.006∗∗∗
(0.001)
0.000
(0.002)
−0.001
(0.002)
0.002∗∗∗
(0.001)
0.000
(0.000)
−0.015
(0.013)
−0.036
(0.031)
−0.107∗∗∗
(0.015)

-0.092∗
(0.052)
-0.103∗∗
(0.045)
0.700∗∗∗
(0.047)
-0.101∗
(0.061)
-0.142∗
(0.075)
-0.062
(0.074)
-0.043∗
(0.024)
0.047
(0.124)
0.033
(0.063)
-0.027
(0.086)
-0.051
(0.058)
-0.130∗∗
(0.054)
0.128∗∗
(0.062)
0.112∗∗
(0.050)
0.014
(0.032)
-0.048
(0.031)
-0.016
(0.030)
-0.023
(0.016)
-0.12∗∗∗
(0.001)
4.688∗∗∗
(0.475)
-3.313∗∗∗
(0.694)
0.211∗
(0.078)

Y
36,148

Y
36,148

Y
36,148

treat
Multiracial
Non-Hispanic Asian
Non-Hispanic Black
Non-Hispanic Native Am/Pacific Islander
Non-Hispanic White
Other RaceEthnicity
male
other gender
married
separated
single, never married
widowed
some high school
high school diploma
some college
some grad/professional school
grad/professional degree
log(pop)
%degree
emp rate
gini
Constant
Survey Year Fixed Effects
Observations

Notes: More granular race/ethnicity variables reflect changes in demographic data collected in later waves
of the HFS. ∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01

44
Electronic copy available at: https://ssrn.com/abstract=3293988