Families of Austerity: Intergenerational Spillovers of Income Loss in Great Britain - OSF

Families of Austerity: Intergenerational Spillovers
                of Income Loss in Great Britain

                    Gabriele Mari∗                          Renske Keizer
             Erasmus University Rotterdam            Erasmus University Rotterdam

                                          March 3, 2021

                                              Abstract
       We study the intergenerational spillovers of income shocks. Compared to income
       boosts, income losses due to policy change have been seldom examined via an inter-
       generational lens. Besides, research on income boosts has centred around parental
       investments of time and money, and has largely focused on maternal inputs during
       early and middle childhood. To complement that, we show how income losses may
       spill over via financial hardship, psychological distress, and parenting. We consider
       both maternal and paternal inputs and highlight how shocks timed around chil-
       dren’s adolescence can affect socio-emotional skills that are key to long-run out-
       comes.
       We analyse income losses following tax-benefit reform in Great Britain in the pe-
       riod 2009-2019 (UK Household Longitudinal Study). Based on an instrumental-
       variable approach, our findings show that benefit income losses stiffened financial
       hardship, particularly in the form of housing arrears and subjective worries. These
       are accompanied by worsening maternal mental health, less effective parenting by
       both mothers and fathers, and increased problem behaviour among their adoles-
       cent children. Benefit income loss also seems to push parents into employment,
       but effects suggest neither a substantial re-direction of time from the household to
       the market nor do labour earnings offset benefit income losses money-wise. Find-
       ings thus speak to debates on the consequences and timing of income shocks for
       children and family environments, bringing to the fore the intergenerational con-
       sequences of welfare cutbacks.
   ∗
     E-mail: mari@essb.eur.nl. The present study was supported by a grant from the Netherlands Or-
ganization for Scientific Research (NWO MaGW VIDI grant no. 452-17-005 to R.K.) and by a grant from
the European Research Council (ERC StG grant no. 757210 to R.K.). We would like to thank Jane Wald-
fogel, Ariel Kalil, two anonymous referees, as well as participants at the ECSR 2019 in Lausanne and
in seminars at NIDI-KNAW and Erasmus University Rotterdam, for their comments and feedback on
earlier versions of this paper. The study uses data from UKHLS Understanding Society (University of
Essex [ISER], 2020a,b) and the Family Resources Survey (Office for National Statistics [ONS], 2019),
accessed via the UK Data Archive. Any errors or omissions are the authors’ own.

There is ample evidence of correlations between family income, family environments,
and child development (for reviews, Heckman & Mosso, 2014; Almond et al., 2018;
Cooper & Stewart, 2020). Assessing how much these intergenerational correlations are
causal or not, and what mechanisms drive them, can inform timely policy intervention,
especially in times like these of exceptional income volatility. Income drops might fol-
low, for example, the expiration of temporary economic stimulus tied to the COVID-19
pandemic (e.g. Ganong et al., 2020; Emmerson et al., 2021). Yet, income losses due to
policy change, and especially benefit cuts, have been seldom examined causally and
with an intergenerational lens. This holds true despite the recent wave of cuts that, al-
though not uniformly across countries, followed the recession of 2008/9 (Alesina et al.,
2019).
In this paper, we tackle the intergenerational spillovers of income loss as triggered by
tax-benefit reform in Britain in the period 2009-2019. Among high-income countries
adopting an austerity agenda in that period, the UK stood out for its cuts to welfare
payments via tax-benefit reform (Fetzer, 2019; Alesina et al., 2019). Family cash ben-
efits get the lion share of social expenditure for working-age households in the UK
(Gornick & Smeeding, 2018) and some key benefits subject to reform, like Child Bene-
fit and Tax Credits, mainly accrue to families with children. Similar to the US and other
Anglophone countries, most provisions at the core of the British safety net are means-
tested, with the poorest half of households having 85% of all of such “legacy” entitle-
ments (Browne et al., 2016; Brewer et al., 2019). This makes austerity-ridden Britain
an exemplary case for studies on the spillovers of income loss across generations, as
child outcomes in low-income families are typically the most responsive to variation in
family income (e.g. Milligan & Stabile, 2011; Dahl & Lochner, 2012; Aizer et al., 2016).
We can rely on high-quality panel data from the UK Household Longitudinal Study
(UKHLS), featuring a large sample of parents and children, as well as precise infor-
mation on income and benefit receipt (Fisher et al., 2019). We further match these data
with estimates of program-specific benefit cuts compiled by previous studies (Beatty &
Fothergill, 2018). This allows for the identification of the effects of income loss spurred
by tax-benefit reform (e.g. Fetzer, 2019) via an instrumental-variable approach.

                                            1

Our first contribution concerns income shocks themselves. Income shocks linked to
child outcomes have either been income boosts brought by welfare expansion or in-
come losses brought by parental layoffs. Studies on boosts have found positive effects
on child health, skill formation, and on long-run outcomes such as completed educa-
tion (e.g. Milligan & Stabile, 2011; Dahl & Lochner, 2012; Hoynes et al., 2016; Aizer et
al., 2016; Bastian & Michelmore, 2018). Income losses, on the other hand, have largely
been discarded as a channel via which parental layoffs may affect the same outcomes
(cf. Oreopoulos et al., 2008; Rege et al., 2011; Stevens & Schaller, 2011; Hilger, 2016). Yet,
earnings losses after job loss are often cushioned by unemployment benefits or other
financial transfers (e.g. Rege et al., 2011; Hilger, 2016). Partly independent from any in-
come loss, in addition, other mechanisms such as worsening parental health or height-
ened chances of divorce might be triggered by layoffs and influence children (Rege
et al., 2011; Eliason, 2012; Mendolia, 2014; Huttunen & Kellokumpu, 2016). Hence,
studies on income loss following layoff are hardly informative on the intergenerational
spillovers of income loss per se. By examining income loss due to tax-benefit reform,
our study fills this gap and mirrors previous studies on income boosts due to welfare
expansion.
We also make three contributions on the mechanisms underlying the intergenerational
spillovers of family income. First, family income shocks are passed on to children via
their parents. There are well established causal connections between family income and
parental investments in goods and services for the child, and in time spent with the child
or in the labour force (e.g. Lundberg et al., 1997; Carneiro & Ginja, 2016; Jones et al.,
2019; Bastian & Michelmore, 2018; Bastian & Lochner, 2020). When lack of income is
concerned, though, stress can be another conduit for intergenerational spillovers. A vast
literature on “family stress”, particularly in developmental psychology and sociology,
documents how lack of income and financial hardship associate with poorer parental
mental health, strained family relationships, and less effective parenting (for reviews,
Conger & Donnellan, 2007; Masarik & Conger, 2017). Questions have arisen on the ex-
tent to which income causes financial and psychological distress, or the latter can also
manifest independently from lack of income (e.g. Yeung et al., 2002; Gershoff et al.,

                                              2

2007; Treanor, 2016; Schenck-Fontaine & Panico, 2019; Clark et al., 2020). Nonetheless,
causal assessments are still few and far between (Gennetian et al., 2008; Masarik &
Conger, 2017), particularly in connection with policy change. Related, studies have in-
variably assessed maternal responses to income shocks (e.g. Milligan & Stabile, 2011;
Boyd-Swan et al., 2016; Bastian & Lochner, 2020), whilst much less is known on pa-
ternal responses. Within a burgeoning literature on fathers’ contribution to child de-
velopment, recent evidence suggests that paternal psychological distress and strained
parenting practices can harm their children’s socio-emotional adjustment (e.g. Le &
Nguyen, 2017; Van Lissa et al., 2019; Van Lissa & Keizer, 2020). None have linked such
paternal inputs to income shocks so far, besides studies on job loss (e.g. Rege et al.,
2011; Mendolia, 2014). Finally, pertaining to the timing of income (e.g. Carneiro &
Ginja, 2016; Carneiro et al., 2021), we focus on adolescence. Adolescence is a sensi-
tive period of the life cycle when it comes to socio-emotional development1 . Income
shocks have been linked to adult-life outcomes (e.g. completed education) and socio-
emotional skills are well-known predictors of such outcomes (Heckman et al., 2006;
Currie, 2009; Attanasio et al., 2020), yet we lack evidence on income shocks and socio-
emotional development itself – particularly during adolescence (cf. Milligan & Stabile,
2011). This motivates us to investigate adolescence as a candidate “missing middle”
in the relation between family income and children’s adult-life outcomes (e.g. Currie,
2020).
Our main findings are that income loss, fuelled by tax-benefit reform, has economic,
psychological, and behavioural consequences that span across generations. Exposed to
austerity measures, both mothers and fathers experience more financial hardship, par-
ticularly in the form of housing arrears, and their subjective outlook on household fi-
nances worsens. Maternal mental health is negatively impacted across a variety of mea-
sures, more consistently so than paternal mental health. Adolescent socio-emotional
development is hampered too, similarly for boys and girls. Whilst evidence on strained
parent-child relationship is inconclusive, we find suggestive evidence of less effective
   1
    Such sensitivity is testified, among others, by studies of brain plasticity (e.g. Nelson et al., 2005;
Blakemore, 2008; Crone & Dahl, 2012) and research on the onset and incidence of psychopathology
(e.g. for the UK, Patalay & Fitzsimons, 2018, 2021).

                                                    3

parenting – harsher among mothers and lower in warmth and consistency among fa-
thers – that could drive the intergenerational spillovers of income loss. Differently, ef-
fects on parental labour supply are modest and unlikely to shift intra-household in-
vestments, be it by substituting time at home with time in paid work or by cushioning
benefit income loss with market earnings.
On income shocks, our findings for income losses mirror those of income boosts on
similar outcomes, comparing welfare cutbacks in our setting to welfare expansion in
past studies (e.g. Milligan & Stabile, 2011; Boyd-Swan et al., 2016). As in the case of ex-
pansions, low-income households drive the effects in our setting. There is evidence of
symmetry, therefore, between the intergenerational spillovers of positive and negative
income shocks. Our findings go beyond such symmetry though, in one important way.
Studies on boosts have regularly pointed out that a family’s permanent income is the
most productive for child development, and that policies better boost family income
conditionally on specific child-related investments (Mayer, 1997; Heckman & Mosso,
2014; Del Boca et al., 2016). In our setting, however, income loss is unlikely to shift per-
manent income at the margin, due to the temporary nature and size of the cuts. Further,
cuts touched upon programs that are unconditional on child-related investments. We
thus suggest that, when considering psychological distress rather than intra-household
investments, temporary and unconditional income shocks can have intergenerational
spillovers. This finding falls in line with a large literature on the psychological effects of
cash transfers on adults and adolescents, well established in low- and middle-income
countries (e.g. Baird et al., 2013; Haushofer & Shapiro, 2016; Ridley et al., 2020). Our
evidence further informs current policy debates on temporary changes to safety nets:
whilst we currently witness a wave of welfare expansion, inverting the route with cuts
(e.g. Emmerson et al., 2021) may impose further stress across generations.
On mechanisms, in fact, our findings suggest that the workings of family stress are
partly causal. We show that income loss can trigger financial hardship and thereby
psychological distress and disrupted parenting (cf. e.g., Schenck-Fontaine & Panico,
2019; Clark et al., 2020). Models of children’s skill formation could thus benefit from
integrating intra-household investments and stress, rooted in income shocks, as in re-

                                              4

cent appraisals in economics (Cobb-Clark et al., 2019) and following a longer tradition
in developmental psychology (Conger & Donnellan, 2007; Masarik & Conger, 2017).
In this respect, results also point to adolescence as a sensitive period for stress mech-
anisms. Recent studies have highlighted that parental income during adolescence is
more strongly linked to adult outcomes than previously thought (Carneiro et al., 2021),
and yet parental investments are largely inelastic to income during the same period
(Carneiro & Ginja, 2016). We suggest that family stress may outweigh parental invest-
ments during adolescence, at least in response to income shocks and with children’s
socio-emotional development causally downstream. Last, maternal and paternal re-
sponses to income shocks may differ, the latter showing somewhat more resilience
in terms of mental health. This echoes findings from studies on job-and-income loss,
showing that fathers are adversely affected by job loss but largely not because of the
resulting income shock (e.g. Rege et al., 2011). Nevertheless, that less effective par-
enting is found in both mothers and fathers suggests that both can contribute to the
intergenerational spillovers of income shocks, at least via this particular channel.
The paper is structured as follows. Section 1 provides background information on tax-
benefit reform in Britain. In Section 2, we present data and samples, measures of income
loss and our instrument, as well as the outcomes in this study. Section 3 illustrates the
econometric approach and discusses the identification assumptions underlying our in-
strumental variable. The main findings are presented in Section 4, followed by sensi-
tivity checks (Section 5). We then discuss our results and conclude.

1.   Background: Tax-benefit reform in Britain after the Great Recession

After the Great Recession, the UK embarked on tax-benefit reform with the proposed
aim of lowering the budget deficit and fostering gainful employment. Culminated with
the Welfare Reform Act of 2012, reforms mainly touched on seven programs, namely
Child Benefit, Working Tax Credit, Child Tax Credit, Local Housing Allowance, Job-
Seeker’s Allowance, Income Support, and Employment and Support Allowance. The
last six are all means-tested programs and together constitute the so called “legacy
system” at the core of the British safety net. Around 1/3 (≈ 7 million) of working-age
households receive at least one of these transfers (Browne et al., 2016; Brewer et al.,

                                            5

2019). Households with children make up to 51% of all households on legacy benefits
(Brewer et al., 2019) and are the sole eligible to receive Child Benefit.
Tax-benefit reforms restricted eligibility, froze transfer levels or their up-rating, and
curtailed entitlements (Beatty & Fothergill, 2018; Fetzer, 2019). Families with children
were affected first and foremost by changes to Child Benefit, as well as Working Tax
Credit and Child Tax Credit (Tax Credits, hereafter). Child Benefit is an unconditional
transfer paid to families for each child under 19 that is still in school or further edu-
cation. From April 2011, payments were frozen at their current rates for the following
three years. Starting January 2013, transfers were progressively withdrawn2 from more
affluent households, i.e. those including at least one earner of more than 50,000 GBP
in annual pre-tax income (roughly twice the median in the period, Fetzer, 2019). Tax
Credits, on the other hand, are in-work earning supplements that mainly accrue to low-
and middle-income families, particularly targeting lone parents (similar to the EITC in
the US, e.g. Brewer & Hoynes, 2019). Among other changes, coverage of childcare costs
was lowered from April 2011, and work requirements were tightened for members of
couples with children from April 2012. Together with changes to Child Benefit, these
measures are estimated to have affected between 15 to 25% of UK households (Fet-
zer, 2019). Tax Credits were further amended in 2016-2017, for example, by limiting
the child element of the tax credit to two children for new births (so called “two-child
limit”).
Other than Child Benefit and Tax Credits, Local Housing Allowance was also subject
to cuts from April 2011. Local Housing Allowance is a housing benefit paid to low-
income renters in the private- and social-rented sectors in the UK. With the reform, the
eligibility threshold was lowered from the median to the 30th percentile of the area-
specific rent, to the detriment of more than 770,000 households (Fetzer et al., 2020).
Whilst this change applied to private renters, social renters were instead hit by the so
called “bedroom tax” – a downward adjustment of Local Housing Allowance, targeting
tenants with spare bedrooms “not justified” by the size and age composition of the
   2
    Affected households included at least one earner above 50,000 GBP, with a taper rate of 1% for each
additional 100 pounds over the threshold. Child Benefit was thus completely withdrawn from house-
holds above the 60,000 GBP threshold (HM Revenue and Cutsoms [HMRC], 2013).

                                                  6

household (see, e.g, Fetzer, 2019). The bedroom tax affected an estimated 460-660,000
households across the country (Beatty & Fothergill, 2016; Fetzer, 2019).
Finally, Local Housing Allowance, the rest of legacy benefits, and Child Benefit were
all subject to a sequence of transitory cuts (e.g. Beatty & Fothergill, 2018). 1% up-rating
substituted adjustment by inflation for most benefits, for three years starting in 2013-
2014 (two years, starting in 2014-2015, for Local Housing Allowance and Child Benefit).
This was paired together with a benefit cap for the same period3 . The cap, still in place
to this day, limits the amount of total benefit income each household can claim per year
(Kennedy et al., 2016). Eligibility depends on which benefits are currently claimed by
household members, total benefit income out of benefits affected by the cap, compo-
sition of the household (whether a single individual or other), and area of residence
(inside or outside London). In 2016-17, the benefit cap was renewed and expanded to
affect more claimants, accompanied by a further four-year benefit freeze.
Low- and middle-income households have been affected the most by tax-benefit re-
form. The poorest fifth of British households derives an estimated 50-60% of their gross
household income from state benefits, a figure that progressively declines moving up
the distribution (Fisher et al., 2019). At the bottom of the income distribution, state
benefits cushioned earning losses in the immediate aftermath of the Great Recession
(Cribb et al., 2017; see also Cribb et al., 2018; Avram et al., 2019). Yet income losses
emerged after 2011-2012, following tax-benefit reforms. Falls in benefit receipt, in par-
ticular, lead to an estimated 4% net household income loss for households in the poor-
est fifth of the family income distribution (Cribb et al., 2018). Benefit income fell more
sharply among families with no earners (ibidem) and, among those with children,
single-parent households were particularly affected (De Agostini et al., 2018).

2.       Data and measures

2.1.      Data

We use data from waves 1 to 10 of the UK Household Longitudinal Study (UKHLS,
University of Essex [ISER], 2020a), covering the period 2009-2019. UKHLS is a large
     3
    The benefit cap applied to recipients of Child Benefit, a string of out-of-work benefits, and legacy
benefits. Among other exemptions, however, the cap did not apply to households with at least one mem-
ber qualifying for Working Tax Credit (for more details, see Kennedy et al., 2016).

                                                   7

household panel survey that comprised around 40,000 households at its start in 2009.
We derive our Parent Sample from the core questionnaire administered to adults age
16 or over. This is coupled with a Youth Sample derived from the Youth questionnaire,
a separate survey of household members aged 10 to 15. Our analysis thus encompasses
parents and their adolescent children. These are then matched to a previously compiled
dataset4 on the intensity of tax-benefit reforms in each Local Authority District (Beatty
& Fothergill, 2018). Local Authority Districts (LADs) are sub-national local govern-
ment units, and Great Britain counted 371 of them as of April 2019. We obtain LAD
identifiers in UKHLS (University of Essex [ISER], 2020b) to match the two datasets.
Given that the most complete data on welfare reforms cover Great Britain only, our
analyses exclude Northern Ireland5 .
To define our samples, we start from the Youth questionnaire. Measures for our child
outcomes of interest are only available in odd waves. Once limited to those waves and
excluding Northern Ireland, our starting sample consists of 11,105 adolescents. These
are adolescents we can match to their biological, step- or adoptive parents, for an ini-
tial total of 6,988 mothers and 5,214 fathers. We apply three sample restrictions. In the
Parent Sample, we exclude 517 person-wave observations for parents past age 64, for
welfare cutbacks applied to the working-age population. Also in the Parent Sample,
we exclude 212 interviews that were conducted in 2020, to prune (outlier) responses
to the COVID-19 pandemic and the first lockdown. Finally, we deploy listwise deletion
in each sample.
As a result of these procedures, our final samples comprise 8,234 adolescents (12,881
person-wave records), 5,423 mothers (34,411 person-wave records), and 3,174 fathers
(18,948 person-wave records). Panels are unbalanced for each of the three groups but,
whilst adolescents are only observed in odd waves, we elected to keep both odd and
even waves for the Parent sample to harness the most information possible. Sample
counts, nonetheless, drop considerably once we apply our sample restrictions. Miss-
   4
      This dataset is publicly available at https://www4.shu.ac.uk/research/cresr/ourexpertise/the
-uneven-impact-of-welfare-reform.
    5
      Similar estimates for the toll of welfare reforms were also made available for Northern Ireland
(Beatty & Fothergill, 2013), yet only covering reforms in the early 2010s. Besides, a change in LAD identi-
fiers for Northern Ireland (from Wave 6 onwards in UKHLS) impedes matching the two datasets without
further assumptions.

                                                    8

ingness and differential attrition are key concerns. Missing values are largely concen-
trated on our instrument, which combines external data with UKHLS info on benefit
receipt. By design, parents will be excluded if they were first interviewed after the date
of the first reform in our analysis (April 2011), as we cannot trace back their benefit
receipt up until that point. Our sample is thus skewed towards early entrants in the
panel, which previous studies found to be “reassuringly similar” to Census data from
2011 (Lynn & Borkowska, 2018). Besides, similar to studies on attrition in UKHLS (ibi-
dem), we find that chances of participation in the analytical (Parent) sample are lower
for men, younger age groups, people on lower incomes at first interview, and in the
Greater London area. The under-representation of low-income families, in particular,
might imply that our estimates of the toll of tax-benefit reform should be regarded as
conservative. On attrition, further, one previous study has shown that private renters
are more likely to drop out from UKHLS than homeowners, and even more so if ex-
posed to the 2011 cut to Local Housing Allowance (Fetzer et al., 2020). Once again, our
estimates of reform-induced income losses might therefore be conservative, particu-
larly for outcomes related to housing.

2.2.   Measuring benefit income loss

We focus on benefit income loss and use income data from UKHLS (Fisher et al., 2019)
to derive, first, a household measure of annual benefit income. We sum monthly income
amounts from seven different sources, namely the six programs composing Britain’s
legacy system and Child Benefit. UKHLS provides monthly equivalents of benefit in-
come, derived from original amounts that respondents most often report on a weekly,
fortnightly, monthly or annual basis6 (Avram et al., 2019). Further, whenever benefit
receipt was joint within two-parent households, we elected to assign the total sum to
each parent7 . Total monthly benefit income is then multiplied by 12 to obtain a measure
   6
     For our Parent Sample, original receipts for Tax Credits and Housing Benefit were most often re-
ported on a weekly basis, Child Benefit on a monthly basis, and Income Support, Job-Seeker’s Allowance,
and Employment and Support Allowance were most often reported fortnightly.
   7
     In our Parent Sample, around 18% of person-wave records register joint receipt of Child Benefit,
16% of Child Tax Credit, 6% of Working Tax Credit, and around 4% of Local Housing Allowance; for all
others, joint receipt is mentioned in less than 1% of records. Throughout, we use individual measures
of benefit income for both descriptives and estimation and, hence, we do not run the risk of counting
twice income from the same benefit receipt within each household. We investigate alternative codings

                                                  9

of annual benefit income for each parent i in each wave w (BINCOMEi,w ).
We then compute wave-by-wave benefit income gains and losses for each parent. We
take the first difference of BINCOMEi,w , subtracting past benefit income (i.e. in the pre-
vious available wave) from current benefit income in each wave Allison (2019). All first
differences with a positive sign, signalling benefit income gains, are summed over each
individual panel to obtain a cumulative measure of benefit income gains (∆+
                                                                          BINCOMEi,w ).

We then take the absolute value of all first differences with a negative sign and sum
them to obtain a cumulative measure of benefit income losses (∆−
                                                               BINCOMEi,w ). Each cu-

mulative delta is set to 0 when the other delta expresses a quantity different from 0,
and both deltas equal 0 when no change in BINCOMEi,w was recorded across waves.
Having measured these deltas in the Parent Sample, we can assign them to children
in the Youth Sample, matching on household and wave. We elected to match children
to the income losses of their mothers, as around 39% person-wave observations in the
Youth Sample do not report a paternal id number that can be matched to fathers in the
Parent Sample (but see Section 5 for sensitivity analyses).

                                  BINCOMEi,w might respond not just to tax-benefit re-
As observed, benefit income loss ∆−
form, but also to changes in labour supply and earnings, household composition, per-
sonal health, and so forth. Similar to previous studies on welfare expansion (Milli-
gan & Stabile, 2011; Dahl & Lochner, 2012), we concentrate on variation due to policy
change using an instrumental-variable (IV) approach. We specifically link income loss

 BINCOMEi,w to the austerity measures detailed in the previous sections, relying on esti-
∆−
mates of welfare cutbacks from previous studies (Beatty & Fothergill, 2016, 2018; for a
previous application, Fetzer, 2019).
We follow a procedure in four steps. First, data on welfare cutbacks provide us with
the estimated financial loss for each tax-benefit reform and with the estimated number
of affected households, separate by Local Authority District. These estimates are based
on official statistics pulled from sources such as the Treasury and the Department for
Work and Pensions (DWP) (for full details, please refer to the Appendices in Beatty &
Fothergill, 2016, 2018). By dividing the estimated annual financial loss by the number of
households affected, we get the annual average loss per affected household for a given
of benefit income in sensitivity analyses.

                                             10

reform and in a given district (Beatty & Fothergill, 2016: 12). Importantly, larger values
reflect not just larger cuts for a given benefit, but also the size and features of claimant
pools across districts. We will account for this later in our econometric approach.
The second step is to identify those likely exposed to such losses in UKHLS. In line with
previous studies (Fetzer, 2019), we consider an individual “exposed” to a given tax-
benefit reform if they are recipients of such tax-benefit program(s) in all available waves prior
to the reform in question (see Section 5 for alternative choices and sensitivity analyses).
Whenever possible, we further narrow it down to identify those most likely treated by
the reform. For example, Child Benefit was frozen for three years in April 2011, but the
main financial loss stemmed from the effective withdrawal of Child Benefit from high-
earning households starting in January 2013. Exploiting this cut-off (i.e. at least one
member with gross earnings above 50,000 GBP prior to 2013), we were able to identify
the group likely affected by such policy change.
Table 1 provides an overview of all the reforms we cover, their timing, the definition of
“exposed group” we deploy, and the (Parent) sample share for each exposed group. In
a third step, we match our external data to UKHLS members. Each respondent in the
Parent Sample is assigned the simulated yearly loss in benefit income for a given policy
change, based on the Local Authority District they reside in and on whether or not they
belong to the group exposed to such policy change. For example, a sample member
residing in Liverpool around the time of the first reform of Tax Credits (April 2011),
who continuously received Child Tax Credit and/or Working Tax Credit prior to April
2011, is assigned the estimated annual benefit income loss for a Liverpool household
in relation to such reform (i.e. 961 GBP).
Fourth and last, we allow our instrument to vary over time. Reforms kick in at a specific
point in time, as reported in Table 1. It follows that for all survey interviews prior to
the starting date of the reform in question, our instrument is set to 0. Further, similar
to our observed variable ∆−
                          BINCOMEi,w , we make it such that simulated benefit income

loss, our instrument, also adds up cumulatively over the panel. The third column of
Table 1 reports the time frames over which we added up the yearly amounts. Some
tax-benefit reforms have a temporary duration of 2 to 4 years and therefore our cumu-

                                               11

lative sums run over such a period. For all others, mainly reforms that became effec-
tive prior to April 2016, we make a conservative choice following Beatty and Fothergill
(2016). Their computations for such reforms reflect the expected outturn up to March
2016, and therefore we stop summing up the corresponding losses at that point in time
– notwithstanding the fact that some of these policy changes might have been more
permanent.

2.3.   Outcomes

Turning to outcomes, we sought a comprehensive picture of family stress, from parents
to children. We first consider parental mental health via two self-reported measures,
namely SF-12 and GHQ-12. The mental health questionnaire comprised in the 12-item
Short Form (SF-12) assessment is a common screening tool for pyschopathology (Ware
et al., 2001; validated for the UK in e.g. Jenkinson & Layte, 1997). There, answers to
six items are recoded to obtain a score ranging from 0 (low functioning) to 100 (high
functioning). The 12-item version of General Health Questionnaire (GHQ-12) is an-
other widely used screening instrument for mental disorders, validated internationally
(e.g. Werneke et al., 2000). The twelve items tap into multiple aspects of psychologi-
cal well-being, from concentration and sleep to confidence and depression. The sum of
scores (0 to 3) for each item provides us with a Likert measure of mental health, rang-
ing from 0 to 36, the latter score indicating the maximum level of distress. We use both
GHQ-12 and SF-12 to avoid conclusions that inherit biases specific to a single measure
(e.g. Brown et al., 2018). We reverse code the GHQ-12 measure, so that higher scores
in both SF-12 and GHQ-12 indicate better health. Both outcomes are standardised with
respect to sex-specific means for ease of interpretation.
Second, we follow previous studies on family stress and consider both “objective” and
“subjective” measures of financial distress (e.g. Schenck-Fontaine & Panico, 2019). We
examine housing arrears with two binary variables, one for rent and one for bills ar-
rears. Both outcomes are coded 1 if parents mention being behind some or all pay-
ments, and 0 otherwise. Beyond housing, we consider food expenditure. In each wave,
parents are asked to report the amount of money spent in food and groceries from su-
permarkets, other food shops or markets. We deflate expenditures at 2019 prices and

                                           12

take the log for ease of interpretation. As for subjective financial worry, we dichotomise
responses to the question “How well would you say you yourself are managing finan-
cially these days?”. Those who are “just about getting by” or that find it “quite or very
difficult” are coded 1, whereas those who are “doing alright” or “living comfortably”
are coded 0.
Outcomes in the Youth Sample are meant to capture socio-emotional problems and
the quality of parent-child relationships. For the former, we rely on 20 items out of
the Strengths and Difficulties Questionnaire (SDQ, e.g. R. Goodman, 1997). This is an
extensively validated screening tool for psychopathology in children and adolescents
(for the UK, e.g., A. Goodman & Goodman, 2009), largely used in the literature on
family stress (e.g. Kiernan & Huerta, 2008; Berger & Houle, 2019) and on skill for-
mation (e.g. Attanasio et al., 2020). Comparable measures of problem behaviour have
also been adopted in studies on the intergenerational consequences of welfare expan-
sion (Milligan & Stabile, 2011). The questionnaire is administered to adolescents them-
selves, reducing the risk that common-method bias might inflate correlations between
parental and child reports. As recommended for population-based, non-clinical sam-
ples (A. Goodman et al., 2010), we construct two summary scores, one for internalising
problems and one for externalising problems. The first taps emotional symptoms and
peer problems, the second sums up conduct problems and hyperactivity/inattention.
The two scales are further standardized with respect to their sex-specific means, for
ease of interpretation.
As for parent-child relationships, we rely on two items asking adolescents to report
the frequency with which they “talk about things that matter to you” or “quarrel” with
their parents. Only a sub-sample of adolescents could answer these question with refer-
ence to their fathers, given that one-parent households are overwhelmingly headed by
single mothers. We do not restrict our adolescent sample, therefore, to young respon-
dents answering both items, to avoid conditioning on family structure. We report both
mother- and father-related measures, acknowledging lost observations for the latter
(480 person-wave records for boys, 477 for girls). All measures are dummy-coded, set-
ting “hardly ever” to 0 and “less than once a week”/“more than once a week”/“most

                                           13

days” to 1. Given that these are admittedly crude measures, we also explore richer
data on parenting in the Parent Sample. These data are only available for parents of 10-
year-olds though, and only from Wave 3 onwards, and we will present these auxiliary
analyses in Section 3.2.
Together with parenting measures, finally, Section 3.2 also explores aforementioned
trade-offs between benefit receipt and labour supply in the Parent sample. We examine
the latter both at the extensive margin, with a binary indicator for whether parent i is
employed or not in wave w, and at the intensive margin, using total weekly working
hours (conditional on employment). We consider substitution dynamics, first, estimat-
ing the effect of benefit income loss on individual annual earnings. Second, we consider
whether benefit income loss spurs parents to switch across benefits. If parents were
able to cushion income shocks by moving strategically across the benefit system (e.g.
Petrongolo, 2009), estimates of policy-induced income loss could be biased downward.
Hence, we build a binary indicator taking value 1 if parents receive a new benefit in
wave w, “new” meaning it was not reported in the previous available wave, while they
simultaneously ceased to receive those benefits they reported in the previous wave.

3.     Methods

3.1.    Econometric approach

To study the effects of benefit income loss on family stress, we start from the following
regression specification estimated via generalised least squares (GLS), namely:

         Yi,w = α1 ∆−                +             0
                    BINCOMEi,w + α2 ∆BINCOMEi,w + Xi,w δ + φt + θm + ωd + µi + υi,w    (1)

where the outcome Yi,w is one of the markers of family stress for a parent i in wave w.
Negative and positive changes in benefit income are obtained via the aforementioned
first-differencing (Allison, 2019). They are expressed, respectively, by ∆−
                                                                          BINCOMEi,w and

 BINCOMEi,w . Both are indexed at 2019 prices and divided by 1,000. In Equation 1, the
∆+
associated coefficients α1 and α2 are computed, first, net of individual outcome trajec-
tories. The vector Xi,w
                    0
                        comprises a quadratic for age to account for overall lifecycle tra-
jectories. Parents across the socio-economic spectrum may also have been on different

                                            14

outcome trajectories prior to tax-benefit reform, for example, due to the Great Reces-
sion and the subsequent recovery. Hence, we also include dummies for net household
income quintile groups as measured at the baseline (first available observation for each
parent) and interact these dummies with a counter for the years preceding parents’ first
exposure to tax-benefit reform. Finally, we include a host of fixed effects: interview year
dummies φt for shared period effects, interview month dummies θm to adjust for sea-
sonality in any of our measures based on monthly reports, and Local Authority District
fixed effects ωd to net out time-invariant geographical heterogeneity. Together with the
error term υi,w , an individual random intercept µi completes the specification to reflect
that repeated observations are nested within individuals in our data. Standard errors
are clustered at the individual level throughout.
Our key coefficient of interest is α1 , expressing the average change in outcome levels
following a 1,000 GBP loss in benefit income. To isolate benefit loss due to exogenous

                                                         BINCOMEi,w with a measure of
policy changes, we build on Equation 1 by instrumenting ∆−
the intensity of welfare reforms described in the previous section. We name the latter
BLOSSi,t,d and follow an instrumental-variable (IV) approach using the generalised
two-stages least squares estimator (G2SLS), as per Equation 2 and 3:

   BINCOMEi,w = β1 BLOSSi,t,d + +β2 ∆BINCOMEi,w + Xi,w ζ + φt + θm + ωd + µi + υi,w
  ∆−                                                                                    (2)
                                     +             0

                  ˆ−
        Yi,w = γ1 ∆                 +             0
                   BINCOMEi,w + γ2 ∆BINCOMEi,w + Xi,w λ + φt + θm + ωd + µi + υi,w      (3)

where the first-stage equation (Equation 2) regresses ∆−
                                                       BINCOMEi,w on the IV BLOSSi,t,d ,

whilst maintaining all the other elements of Equation 1. District fixed effects ωd , in par-
ticular, are crucial to curb our estimates from between-district variation in our IV, re-
lated to larger claimants pools and, thus, to historical deprivation rather than to recent
welfare reforms (Beatty & Fothergill, 2016, 2018). From Equation 2 we then obtain the
predicted value ∆BINCOMEi,w and we include it in Equation 3, in place of the observed
                ˆ−

negative delta. We proceed similarly with Equation 2 and 3 in our Youth Sample, exam-

                                            15

ining how children’s problem behaviour and parent-child relations respond to benefit
income loss8 .
Given the large number of outcomes and hypotheses, we accompany standard p-values
with so called sharpened q-values9 (Benjamini et al., 2006; Anderson, 2008). The latter
adjust for the false discovery rate (FDR), i.e. the expected proportion of rejections that
are false positives in a given set. In line with previous studies (Anderson, 2008), we
compute q-values in four different sets corresponding to the four subsamples (mothers,
fathers, boys, girls). To avoid redundancy, we will only report q-values when they differ
enough from p to cross conventional thresholds of statistical significance (e.g. .05 and
.10).

3.2.    Identification

Equation 3 can provide an estimate (γ1 ) of the causal effect of benefit income loss un-
der a set of assumptions, namely relevance, conditional independence, the exclusion
restriction, and monotonicity (Imbens, 2014). First, to make sure that the IV is relevant,
we assess the extent to which simulated benefit income losses co-vary with observed
benefit income losses. For illustrative purposes, panel a. of Figure 1 averages cumula-
tive losses by quintile of net household income at the baseline and among mothers in
the Parent Sample, pairing observed and simulated (IV) estimates. As expected, bene-
fit income losses are concentrated in the poorest quintiles and monotonically decrease
moving to the richest quintiles. Average observed losses reach a maximum of around
5,000 GBP in the poorest quintile, and around 3,800 GBP in the grand average. Simu-
lated losses follow the same pattern across quintiles, but reach at most around 3,500
GBP in the poorest quintile (2,800 GBP in the grand average), an indication that part
   8
      Given the more narrow age range (10-15) in the Youth Sample, we adjust for lifecycle effects directly
via a full set of age dummies rather than relying on a quadratic.
    9
      In our setting, we prefer q-values to more common Bonferroni corrections for two reasons. Bon-
ferroni corrections assume a worst-case dependence structure among p-values that is close to indepen-
dence, whilst the q-value correction works well with positively dependent p-values too (Benjamini et al.,
2006) - and our setting likely aligns with the latter scenario. Also, Bonferroni-type corrections account
for the family-wise error rate (FWER), i.e. the probability of making even a single Type I error, at the
cost of statistical power. Accounting for the FDR is less stringent, trading off the chance of making some
false rejections for a lesser penalty when testing additional hypotheses. In our setting, we believe we can
tolerate some false rejections and retain our substantial conclusions.
   Stata code is available at http://are.berkeley.edu/~mlanderson/downloads/fdr_sharpened
_qvalues.do.zip.

                                                    16

of the variation in observed losses might be spurious. Table 2 further supports the idea
that simulated losses predict observed ones, reporting first-stage estimates as per Equa-
tion 2. In all main sub-samples, we find sizeable first-stage coefficients in the range .4-.5
(p < .001). The F-statistic is also well above conventional cutoffs (Andrews et al., 2019),
ranging from a minimum of 137.4 for boys to 329.1 for mothers.
We assume, second, that our IV is conditionally independent. Exposure to welfare cut-
backs is not randomly assigned and the “doses” of tax-benefit reform (i.e. non-zero
IV values) are calculated to reflect the size and characteristics of the pool of claimants
in each district (Beatty & Fothergill, 2016, 2018). Hence, in Equation 2 and 3 we ex-
ploit variation in our IV conditional on benefit income gains (∆+
                                                                BINCOMEi,w ) that may

capture time-varying characteristics of benefit recipients, quintile-groups based on net
household income at the baseline, a variety of time-dependent outcome trajectories,
time-invariant district features wiping between-district variation (ωd ), and a random
individual intercept. We prefer the latter to the inclusion of individual fixed effects, as
the latter might produce an unwarranted re-weighting of our estimates (e.g. Løken et
al., 2012; De Chaisemartin & d’Haultfoeuille, 2020; see Appendix 2A for more detail).
We also do not account more specifically for time-varying shocks in the period. Cuts to
Local Authority spending occurred around the same time, affecting disproportionately
more deprived districts (Innes & Tetlow, 2015), yet such shocks are not passed on to
families via benefit income loss. Funding for Sure Start, a flagship early-years educa-
tion programme, was also cut in the same years, with potential detrimental effects on
children (Cattan et al., 2019). Most adolescents in our sample, however, are unlikely to
have been exposed to the long-term fallout of Sure Start, being already in school by the
time Sure Start cuts and closures hastened (around 2011 and 2014, respectively; ibidem:
29). In sum, we consider conditional independence to hold based on the selected set of
covariates, and we discount the role of other district-specific time-varying shocks (but
see Section 5 for other simultaneous policy changes).
Third, the exclusion restriction imposes that any effect of tax-benefit reform would be
passed onto households, first, via benefit income losses. An alternative could be that
families, unexposed to the reforms themselves, were nonetheless hit via contractions

                                             17

in the local economy resulting from the reforms. Fetzer (2019) has found evidence for
such a general equilibrium effect, highlighting reductions in district-level Gross Value
Added (GVA) associated with a measure of reform intensity similar to ours (also based
on Beatty & Fothergill, 2018). Although available GVA time series can only be partially
matched to our UKHLS data, including a measure of year- and district-specific GVA
does not alter our results (see Section 5) and thus enhances the credibility of the exclu-
sion restriction in our setting.
Last, monotonicity in our setting implies that larger benefit cuts, if affecting households
at all, always generate larger benefit income losses. The background for this is that our
estimand of interest is a local average treatment effect (LATE), local in that it gener-
alises to those who experience benefit income losses that would not have occurred – or
been as large – in the absence of tax-benefit reform (compliers). Monotonicity then im-
plies the absence of defiers, those who would instead experience larger benefit income
gains if exposed to larger cuts, and larger losses when exposed to smaller or no cuts
at all. Relying on counterfactuals, monotonicity cannot be tested, but implications can
be derived and assessed empirically. For one, units that have been assigned a larger
IV dose should experience benefit losses at least as large as those of units subject to
more limited doses or no dose at all. Graphically, the cumulative distribution functions
(CDFs) of observed benefit loss should thus never cross and progressively shift, as the
intensity of the IV increases (Angrist & Imbens, 1995). Panel b. of Figure 1 investigates
this pattern, once again focusing on mothers in our Parent Sample for illustrative pur-
poses. We discretised our multivalued IV into meaningful intervals and plotted the
corresponding CDFs of observed benefit income loss. The latter appear to be, by and
large, ever increasing for larger values of the IV, lending confidence to the assumption
of monotonicity in our setting.
Appendix 1A provides additional supporting evidence, characterising likely compli-
ers in our sample. Whilst one cannot observe compliance, it is reasonable to assume
that compliers will be among those households who are both exposed to cuts and ex-
perience benefit income loss. Table 1A compares parents in this group of likely com-
pliers (around 48% of all person-wave observations) against the whole sample on a

                                            18

range of observable characteristics. Women are over-represented as compared to men,
and even more among likely compliers (around 80%) than in the whole sample. This
is largely the byproduct of the substantial proportion of single-parent households,
overwhelmingly (99%) headed by a mother, in the whole sample (around 13%) and
even more among compliers (around 15%). In addition, women’s over-representation
among likely compliers in particular is due to their disproportionate receipt of key ben-
efits in our study, such as Tax Credits. Likely compliers are also less often observed in
paid employment, albeit only slightly in comparison to the whole sample (77% against
79%, respectively), and are more likely to have started their observation period in the
bottom quintiles of net household income, in line with evidence in Figure 1 (Panel a.).
Features of likely compliers in our study, in particular the skew towards households
with lower income and headed by a single mother, are thus in line with previous evi-
dence on the bite of tax-benefit reform in Britain (De Agostini et al., 2018; Cribb et al.,
2018).

4.     Findings

4.1.    Benefit income loss and family stress

Figure 2 displays our main findings, using the IV approach as per Equation 2 and 3.
Starting from parents on the left, we find that maternal mental health worsens in re-
sponse to benefit income loss. For each 1,000 GBP loss triggered by tax-benefit reform,
maternal GHQ-12 scores decrease by 3.7% of a SD (p < .001) and SF-12 scores decrease
by a similar 3% of a SD (p < .001). Estimates for men are more noisy and less consistent
across the two self-reported measures, as a decrease of around 1.1% of a SD in SF-12
scores (p = .295) is coupled with a nil (.01% of a SD) estimate for GHQ-12 (p = .916).
As for economic hardship at the bottom of the panel, mothers report a higher incidence
of rent arrears in response to benefit income loss, of around 0.4 percentage points (p =
.009). Estimates for fathers are nil for rent, but similar to those of mothers for bills. The
chance of reporting arrears with some or all bills increases by around 0.7 percentage
points for mothers (p = .012) and 0.8 percentage points for fathers (p = .005), for a 1,000
GBP loss following tax-benefit reform. Accompanying housing arrears, we find that a
yearly 1,000 GBP benefit income loss leads to a cut of 0.7% in monthly food expenditure

                                             19

among mothers (p = .068, q = .048), an effect we cannot detect for fathers (.01%, p =
.779). Similar effect sizes across parents are also found for subjective financial worry,
whose probability increases by 0.9 percentage points among mothers (p = .003) and
0.7 points among fathers (p = .074, q = .093), respectively.
In the right panel of Figure 2 we turn to adolescents. Socio-emotional problems appear
heightened by benefit income loss. We find that internalizing problems, in particular,
increase by 6.9% of a SD among boys (p = .007) and only 3% of a SD among girls
(albeit p = .159). For externalizing problems, estimates point to an increase of 6.2-7.6%
of a SD among girls (p = .001) and boys (p = .002), respectively. The bottom of the
right panel investigates two measures of parent-child relationships, a possible link via
which family stress trickles down from parents to children. Evidence is not clear-cut in
this respect. Chances of quarrelling with one’s mother increase for boys (0.9 percentage
points), but not for girls (– 0.5 percentage points), and both estimates are noisy (p =
.431 and p = .620). Estimates for talking about things that matter with one’s mother
are also noisy, but point in the expected negative direction (– 1.5 percentage points
for girls, p = .123; – 0.5 percentage points for boys, p = .479). For father-related items,
chances of talking about things that matter decline by around 2 percentage points for
both boys (p = .032, q = .088) and girls (p = .072, q = .104), but so does the chance of
quarrelling (particularly for boys, by around 2 percentage points, p = .094, p = 104).
In sum, findings in Figure 2 paint an overall picture of family stress following income
losses due to tax-benefit reform in Great Britain. Among parents of adolescents in our
sample, we find evidence of accrued economic hardship, particularly in the form of
housing arrears. Benefit income loss, hardship, and subsequent financial worry blend
into a more general worsening of mental health, although much more strongly and
consistently for mothers as compared to fathers. Their adolescent children, age 10 to
15, report more problem behaviour, with similar effect sizes among boys and girls par-
ticularly for externalizing behaviour. Evidence on whether and how parent-child inter-
actions respond to income loss is mixed, however.

                                            20

4.2.   Trade-offs with labour supply or disrupted parenting?

To appreciate the full scope of mechanisms, we consider, first, whether trade-offs might
have ensued between benefit receipt and labour supply. Benefit income loss could push
people into employment, with ambiguous effects on family stress and its consequences
for children. The top of Panel a. in Figure 3 shows that, for a 1,000 GBP loss, both moth-
ers and fathers increase their labour supply by around 1 percentage point (p < .001
and p = .001, respectively). We find positive effects also at the intensive margin, this
time larger for mothers (≈ .4h per week, p < .001) than fathers (≈ .2h, p = .072). These
effects may imply, at best, a modest redirection of time away from home production
and into paid work, following benefit income loss. Moving from time to monetary in-
vestments, we find only limited evidence that benefit income loss might be tempered
by extra annual earnings. Estimates for mothers are noisy (p = .441) and modest, im-
plying a 64 GBP extra earnings per each 1,000 GBP loss in benefit income. Figures for
paternal earnings are larger, yet still stop at an average of around 400 GBP per 1,000
GBP lost (p = .001). We also find little evidence, last, of any “strategic” switching across
benefits following benefit income loss triggered by austerity reforms. Estimates stop at
or below 2 tenths of a percentage point for both mothers and fathers (p = .806 and p =
.146, respectively).
Panel b. in Figure 3 moves on to detailed measured of parenting, described more at
length in Section 3A of the Appendix. While changes in labour supply may indicate
a shift in parental time investments, these more qualitative aspects of parenting are
typically implicated by the literature on family stress. In particular, this scholarship has
pointed to worse behavioural outcomes for children exposed to low warmth, as well as
harsher and less consistent discipline (e.g. Conger & Donnellan, 2007; Pinquart, 2017;
Masarik & Conger, 2017; see also Fiorini & Keane, 2014). Even if only available for the
subsample of parents of 10-year-olds, estimates in Panel b. can thus be considered a
complement to and expansion on previous results on parent-child relationships. We
find that mothers exposed to benefit income loss score around 10% of a SD higher in
terms of parental harshness (p = .032). Fathers, on the other hand, respond to benefit
income loss by scoring lower on warmth (– 10% of a SD, p = .011) and consistency (≈

                                            21

– 9% of a SD, p = .033, q = .063). All other estimates are trivial in size and the null is
not rejected.

5.   Sensitivity checks

We performed a number of checks to assess the sensitivity of our main findings regard-
ing family stress. These checks are presented in Section 4A of the Appendix. Through-
out each figure, specification (1) displays estimates from our preferred model as per
Figure 2, for comparison.
Starting from the Parent Sample, we consider alternative IV definitions in specifications
(2) and (3). In constructing our IV, we have summed cuts over the years for each multi-
year reform, obtaining a cumulative IV that mirrors cumulative (observed) benefit in-
come loss ∆BINCOMEi,w . Whilst we made conservative choices in such counts, assump-
          ˆ−

tions on the timing of reforms could be called into question. Previous studies relying
on the same welfare data did not resort to cumulative measures of welfare cutbacks,
but rather interpreted the latter as one-off shocks (Fetzer, 2019). Specification (2) does
the same, assigning to each exposed group a single value for the projected welfare cut,
from the start of each reform (Table 1) onwards. Estimates are somewhat larger than in
our main specification, in the direction of more stress, notably so for fathers’ GHQ-12
score (– 1.7% of a SD, p = .118). Food expenditures among mothers are an exception
though, reducing to more than half of the original estimate (and p = .633). Similar,
Specification (3) does away with our strict definition of exposed groups, for which
we required individuals to be continuous recipients of a given program prior to its
reform. Some more discontinuous recipients or late beneficiaries fall outside our defi-
nition, but might be exposed to the cuts nonetheless. Besides, some early reforms (esp.
Tax Credits) might have affected eligibility itself, rather than just payment levels, mak-
ing continuous recipients a potentially selective group. To estimate specification (3) we
identify exposed groups as per Table 1, but define exposure as being observed at least
once on each given program prior to its reform. Estimates are often slightly smaller in
this specification, but statistically indistinguishable from their original counterparts.
Specification (4) serves us to assess heterogeneity across reforms. Low-income households
are most likely driving our estimates, being over-represented among “likely compli-

                                            22