THE DYNAMIC EFFECTS OF TAX AUDITS

Arun Advani, William Elming, and Jonathan Shaw*

Abstract—We study the effects of audits on long run compliance behavior
using a random audit program covering more than 53,000 tax returns. Wir
find that audits raise reported tax liabilities for five years after audit, Effekte
are longer-lasting for more stable sources of income, and only individuals
found to have made errors respond to audit. A total of 60%–65% of revenue
from audit comes from the change in reporting behavior. Extending the
standard model of rational tax evasion, we show that these results are best
explained by information revealed by audits constraining future misreport-
ing. Together these imply that more resources should be devoted to audits,
audit targeting should account for reporting responses, and performing au-
dits has additional value beyond merely threatening them.

ICH.

Einführung

AUDITS are a widely used public-policy tool for reduc-

ing corruption (Bobonis, Cámara Fuertes, & Schwabe,
2016; Avis, Ferraz, & Finan, 2018), improving public ser-
vice delivery (Zamboni & Litschig, 2018; Lichand, 2016;
Gerardino, Litschig, & Pomeranz, 2020), ensuring environ-
mental standards (Duflo et al., 2013, 2018), and improving tax
compliance (Kleven et al., 2011; Pomeranz, 2015; Asatryan
& Peichl, 2017; Bergolo et al., 2020; Sarin & Summers, 2020,
unter anderen). But audits are costly, so determining how
many to do and how best to allocate them are key policy
Fragen (Slemrod & Yitzhaki, 2002). In tax, the standard
approach to setting the number of audits is to compare their
costs with the expected missing tax uncovered at audit—
the static gain from an audit (Allingham & Sandmo, 1972;
Kolm, 1973; Yitzhaki, 1987; Bloomquist, 2013). Jedoch,
audits may change taxpayer behavior. A field experiment in
Denmark, which followed taxpayers for a year after audit,
found an increased reported liability worth 55% of the au-
dit adjustment (Kleven et al., 2011). This suggests that static
gains may understate the total gains from audit. Jedoch,
without a longer horizon, it is hard to know by how much,

Received for publication December 16, 2019. Revision accepted for pub-

lication April 8, 2021. Editor: Rema N. Hanna.

∗Advani (Korrespondierender Autor): University of Warwick, CAGE Research
Centre, the Institute for Fiscal Studies (IFS), and the Tax Administration
Research Centre (TARC); Elming: IFS and TARC at the time of involvement
in this work; Shaw: Financial Conduct Authority.

The authors thank Michael Best, Richard Blundell, Tracey Bowler, Mo-
ica Costa Dias, Dave Donaldson, Mirko Draca, James Fenske, Clive Fraser,
Claus Kreiner, Costas Meghir, Gareth Myles, Matthew Notowidigdo, Áureo
de Paula, Andreas Peichl, Imran Rasul, Chris Roth, Joel Slemrod, Hannah
Tarrant, and seminar participants at the Tax Systems Conference, Royal
Economic Society, Louis-André Gérard-Varet, European Economic As-
sociation, Warwick Applied Workshop, OFS Empirical Analysis of Tax
Compliance, International Institute of Public Finance, Econometric Soci-
ety European Meetings, and National Tax Administration Conferences for
helpful comments. We also thank Yee Wan Yau and the HMRC Datalab
team for assistance with data access. This work contains statistical data
from HMRC which is Crown Copyright. The research data sets used may
not exactly reproduce HMRC aggregates. The use of HMRC statistical data
in this work does not imply the endorsement of HMRC in relation to the
interpretation or analysis of the information.

A supplemental appendix is available online at https://doi.org/10.1162/

rest_a_01101.

or even whether this effect is reversed in subsequent years,
as some lab experiments suggest (Maciejovsky, Kirchler, &
Schwarzenberger, 2007; Kastlunger et al., 2009).

This paper studies the long-run effect of tax audits on tax-
payer compliance behavior. We combine confidential admin-
istrative data on the universe of UK tax filers over thirteen
years with a randomised audit programme. We show three
main results. Erste, audits raise subsequent tax reports, Aber
the effect declines to zero over five to eight years. The ag-
gregate additional revenue after audit is at least 1.5 times the
underpayment found at audit, implying substantially more
resources should be dedicated to audit than a static compari-
son would suggest. Zweite, the revenue gain is longer-lasting
for more stable income sources. This highlights the impor-
tance of dynamics for targeting audits, as well as for setting
their level. Dritte, using an event study strategy, we show that
these effects are driven by individuals who were found to be
underreporting, while there is no response for those found to
have reported correctly. These three results can be explained
by a model in which audits provide the tax authority with
information about a taxpayer’s income at the time of audit.
This makes later misreporting more difficult, particularly for
stable income sources.

To estimate the long-run effect, we exploit a random audit
programme run by the UK tax authority (HM Revenue and
Customs, HMRC). Über 53,000 individual tax filers were un-
conditionally randomly selected for audit by the programme
zwischen 1998/1999 Und 2008/2009, allowing us to address
the common concern that audits are typically targeted to-
wards taxpayers believed to be underreporting. Ähnlich zu
Denmark (Kleven et al., 2011) and in contrast to the United
Zustände (Slemrod, Blumenthal, & Christian, 2001; DeBacker
et al., 2018; Perez-Truglia & Troiano, 2018), taxpayers are
not told these audits are random. This is important as tax-
payers may respond differently—likely less—to audits they
know are random, relative to when they think the tax au-
thority is concerned about something on their return. Wir
combine these audit data with data on the universe of UK
self-assessment taxpayers—individuals who self-file taxes
rather than having all tax collected via withholding—from
1998/1999 Zu 2011/2012. This allows us to follow individ-
uals for many years after audit. For our first identification
strategy, we construct a control group for each year of the
programme from individuals who could have been selected
for a random audit that year but were not. We then study the
difference in reporting behavior over time.

Our first result is that dynamic effects are positive and sub-
stantial: taxpayers report higher levels of tax for five to eight
years after audit. We see an initial increase, and then a steady
Abfall, in total tax reported over time. By eight years af-
ter audit there is no difference in average tax paid between
audited and unaudited taxpayers, though differences are not

The Review of Economics and Statistics, Mai 2023, 105(3): 545–561
© 2021 The President and Fellows of Harvard College and the Massachusetts Institute of Technology. Veröffentlicht unter einer Creative Commons Namensnennung 4.0
International (CC BY 4.0) Lizenz.
https://doi.org/10.1162/rest_a_01101

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546

THE REVIEW OF ECONOMICS AND STATISTICS

statistically significant beyond five years. A total of 60%–
65% of the total revenue received as a result of audit comes
from this change in reporting behavior. Taking into account
this effect, tax authorities should do many more audits: ac-
counting for dynamic effects, even random audits provide a
return equal to 80% of their cost to the tax authority. Given the
recent focus on the value of audits purely as a threat (Slemrod,
Blumenthal, & Christian, 2001; Fellner et al., 2013; Dwenger
et al., 2016; Mascagni, 2018; Bergolo et al., 2020; Lichand,
2016); this highlights a benefit of actually performing the
audits.

Zweite, we show that dynamic effects fall to zero slower
for more stable income sources. Pension income, welches ist
highly autocorrelated (“stable”) in the absence of audit, Re-
sponds permanently. At the other extreme, the effect on self-
employment and dividend income returns to zero within three
Jahre. This is important for two reasons. Erste, it has impli-
cations for the targeting of audits. Going after a smaller sus-
pected discrepancy on a more stable income source can have
high returns once dynamic effects are included. Reauditing
is also more likely to produce additional yield for individu-
als with less stable income sources. Zweite, it is relevant for
understanding why people respond to audits, as we describe
below. A natural concern in treating this difference causally,
and using it to interpret behavior, is that individuals with dif-
ferent types of income may respond differently. We account
for this by using pairwise comparisons of income sources
within individuals who have both sources, and we demon-
strate that the less stable source still declines more quickly.
Dritte, we show that audits only change the behavior of
those who are found to have misreported. To do this we use
an event study approach. We compare individuals who were
audited at some point in our sample and who ultimately all had
the same audit outcome, for example were found to be non-
compliant. Allowing for individual and calendar time fixed
Effekte, the comparison is essentially between those whose
noncompliance has already been uncovered by a random au-
dit and those who will have it uncovered in the future. Wir finden
that being audited only changes the behavior of those who
are found to have misreported, and this is true whether or
not they received a penalty. Wichtig, this tells us that the
effect of audits comes not merely from scaring all taxpayers
into paying more, but specifically from changing the behav-
ior of those who were previously misreporting. It also allows
us to rule out audits reducing tax reports, even for those who
were found compliant, in contrast with results using alterna-
tive identification strategies (Gemmell & Ratto, 2012; Beer
et al., 2020).

These results are consistent with audits providing the tax
authority with information at a point in time, which constrains
future misreporting. To see this, we extend the canonical
model of tax evasion (Allingham & Sandmo, 1972; Yitzhaki,
1987; Kleven et al., 2011) to incorporate (simple) dynam-
ics in the response to audit. This allows us to study the dis-
tinct predictions of three different mechanisms that might
drive changes in reporting: (ich) changes in beliefs about the

underlying audit rate or penalty for evasion (“belief updat-
ing“); (ii) changes in the perceived reaudit risk following au-
dit (“reaudit risk”); Und (iii) updates to the information held
by the tax authority (“information”). Kleven et al. (2011) Notiz
that their observed increase in reported tax one year after au-
dit could be explained by some combination of beliefs and
reaudit risk, but they cannot disentangle the two. We note that
a response to belief updating should be permanent, as taxpay-
ers revise the expected cost of noncompliance (up or down).
This is inconsistent with the declining pattern of dynamic ef-
fects we see. A response to reaudit risk would decline over
Zeit. Whether it took the form of a “bomb crater” (Mittone,
2006)—that the probability of audit is lower in the years fol-
lowing an audit before rising back to baseline—or a worry of
higher levels of short-term scrutiny, we should see the same
effect across all income sources. We see a positive dynamic
Wirkung, ruling out “bomb craters,” and we see a differential
decline across income sources, even within individuals, rul-
ing out an effect driven purely by reaudit risk. Instead we
propose a third, novel, possibility. As Kleven et al. (2011)
Notiz, when taxpayers know the tax authority has access to
third-party information about some income source, they are
much less likely to underreport. Ähnlich, when the tax au-
thority performs an audit, it gets a snapshot of income at a
point in time. Implausibly large deviations in reported income
in following years are likely to trigger an audit, because tax
authorities (partly) condition audit selection on differences
between reported income and their expectation of that in-
come based on other sources of information (Advani, 2022).
As time passes, the snapshot becomes less informative about
what current income is likely to be. This is particularly true
for less stable income sources. In this case, we should see a
decline in dynamic effects over time, with less stable income
sources showing a faster decline. We should also only see
responses from individuals who were found to have misre-
portiert, because no new information about the other taxpayers
is revealed to the authority. These are precisely the patterns
that are observed.

Our results imply that audits themselves are important,
beyond the “fear” or “threat” of audit. Much of the recent lit-
erature studying the administration of taxes and the policies
that can improve taxpayer compliance has focused on “letter
experiments”: how different forms and content of informa-
tion provided to taxpayers can change their behavior (see Blu-
menthal, Christian, & Slemrod, 2001; Slemrod et al., 2001 für
early work, and Mascagni, 2018; Alm, 2019; Pomeranz and
Vila-Belda, 2019; Slemrod, 2019 for recent surveys of this
Literatur). These all aim to change the perceived probability
of audit. They have the benefit that they are a very low-cost
policy for a tax authority, yet show substantial (short-term)
gains. Zum Beispiel, Bergolo et al. (2020) find, in the con-
text of VAT in Uruguay, that firms do not respond to the
actual probability of audit when sent letters informing them
davon. Stattdessen, firms increase compliance because thinking
about the audit scares them into compliance. This raises a
question: can high levels of compliance be achieved, while

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THE DYNAMIC EFFECTS OF TAX AUDITS

547

reducing the number of audits, by directing more resources
towards information campaigns? Our results imply that this
is harder than previously thought, as much of the gain from
audit is the change in behavior it promotes. This response is
driven by the information received by the authority through
actually conducting the audit. Threat letters do not provide
this information benefit. To understand any substitutability
with audits, more information is needed on the long-term
effects of such letters: for how long do threats raise com-
pliance, and can repeated threats continue to maintain high
compliance rates?

Im Gegensatz, third-party information is a more direct sub-
stitute for audits. Recent work has shown the importance
(and limits) of third-party information for improving compli-
ance (Kleven et al., 2011; Pomeranz, 2015; Kleven, Kreiner,
& Saez, 2016; Carrillo, Pomeranz, & Singhal, 2017; Slem-
rod et al., 2017; Naritomi, 2019). Since this directly reduces
the information asymmetry between taxpayer and authority,
it will also reduce the information value of audits, welche
drives the dynamic effects. Umgekehrt, for income sources
where third-party information can be hard to come by, au-
dits can be a partial alternative to gathering information from
other sources. They will not only improve contemporaneous
compliance, but also reduce the scope for future noncompli-
ance. This contrasts with work on firms, which finds comple-
mentarity between monitoring and enforcement (Almunia &
Lopez-Rodriguez, 2018).

We find no evidence of “backfire” effects, where audits re-
duce compliance. Worries about backfire effects are common
across areas of tax policy (Perez-Truglia & Troiano, 2018). In
our context they raise the risk that poorly targeted audits may
reduce compliance. Gemmell and Ratto (2012) suggest some
reduction in tax reported by individuals who are audited and
found compliant, relative to individuals not audited. Similar
results are found in the United States by Beer et al. (2020) us-
ing a matched difference-in-difference approach. Our event
study strategy allows for potential differences in unobserv-
able characteristics between compliant and noncompliant
individuals, and finds no backfire. The difference in our
results, compared to existing work, also suggests that unob-
servable differences are important in explaining compliance
behavior. Since we find no reduction in overall tax paid, Es
also suggests that lab experimental evidence of bomb crater
effects is not reflected in real-world settings (Maciejovsky
et al., 2007; Kastlunger et al., 2009), although we note that
not all lab experiments find evidence of such effects (Choo,
Fonseca, & Myles, 2013).

Endlich, we provide a new theoretical mechanism for why
audits have the observed effects. Understanding what moti-
vates compliance is a key question for public policy, und da
are rich debates on the extent to which moral versus economic
calculations drive behavior (Alm, 2019). We focus on the nar-
rower question of why audits affect compliance, and we find
that information is the key. Um dies zu tun, we use evidence from
random audits to look at both the time path of dynamic ef-
fects across income sources and the effects by audit outcome.

Though earlier work has (separately) studied both of these is-
sues, we show how they can be used to understand why audits
change behavior.1 Our results complement those of Bergolo
et al. (2020) and Lichand (2016), who find that the threat of
audit works through fear and belief-updating, jeweils. In
Kontrast, receipt of audit works through a change in ability to
misreport without being caught, an effect that cannot occur
in the absence of actual audit.

The remainder of the paper is organised as follows. Sec-
tion II outlines the policy context and data sources. Section III
provides evidence on who is noncompliant. Section IV shows
how audits affect reporting behavior in overall tax, und von
different income sources. Section V uses an alternative iden-
tification strategy to estimate the impact by audit outcome.
Section VI outlines a model of tax evasion with dynamics
in the response to audits, to show which mechanisms might
rationalise the observed behavior. Section VII concludes.

II. Context and Data

A. The UK Self-Assessment Tax Collection

and Enforcement System

In diesem Papier, we focus on individuals who file an income
tax self-assessment return in the UK. Over our sample pe-
Riod (1999–2012) this comprised around nine million indi-
viduals, one-third of all individual income taxpayers in the
UK.2 Income tax is the largest of all UK taxes, konsequent
contributing a quarter of total government receipts over this
Zeitraum. Most sources of income are subject to income tax, In-
cluding earnings, retirement pensions, income from property,
interest on deposits in bank accounts, dividends, and some
welfare benefits. Income tax is levied on an individual basis
and operates through a system of allowances and bands. Jede
individual has a personal allowance, which is deducted from
total income. The remainder—taxable income—is then sub-
ject to a progressive schedule of tax rates. Tisch 1 zeigt die
share of individuals in our sample reporting nonzero values
for each component of income. When we later study income
components separately, we focus on those components where
mindestens 5% of the population report nonzero values.

Since incomes covered by self-assessment tend to be
harder to verify, there is a significant risk of noncompliance.

1A number of studies consider dynamic effects for one or two years after
audit (Long & Schwartz, 1987; Erard, 1992; Tauchen, Witte, & Beron,
1993; Kleven et al., 2011; Løyland et al., 2019). Concurrently with this
Studie, DeBacker et al. (2018) have a longer (six-year) horizon, and they
also consider income stability, albeit with U.S. audits where taxpayers are
explicitly told they are random, which Slemrod (2019) notes “would likely
trigger different revaluations of how likely a future audit is, and therefore
trigger different behavioral changes” (a similar point is made in Kleven
et al., 2011). Effects by audit outcome are studied by Gemmell and Ratto
(2012) and Beer et al. (2020).

2Filers include self-employed individuals,

those with incomes over
£100,000 (lower at the start of the sample period), company directors, Land-
lords, and many pensioners. The remainder have all their income tax col-
lected directly via withholding, so are not required to file. Note that UK tax
years run across calendar years—we denote tax years using the later year.

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TABLE 1.—SHARE OF TAXPAYERS WITH EACH SOURCE OF INCOME

Income component

Interest
Employment
Self employment
Dividends
Pensions
Property
Foreign
Trusts and estates
Share schemes
Other

Proportion

.587
.482
.375
.370
.300
.136
.048
.010
.002
.030

Annual averages for tax years 1998/1999–2008/2009. Includes only control observations, das ist, those

selected for placebo audit.

Quelle: Authors’ calculations based on HMRC administrative datasets.

Infolge, HM Revenue and Customs (HMRC, the UK tax
authority) carries out audits each year to deter noncompliance
and recover lost revenue. HMRC runs two types of audit: “tar-
geted” (also called “operational”) and “random.” Targeted
audits are based on perceived risks of noncompliance. Ran-
dom audits are unconditionally random from the population,
and are used to ensure that all self-assessment taxpayers face
a positive probability of being audited, as well as to collect
statistical information about the scale of noncompliance and
predictors of noncompliance that can be used to implement
targeting.

The timeline for the audit process is as follows. The tax
year runs from 6th April to 5th April. Shortly after the end
of the tax year, HMRC issues a “notice to file” to taxpayers
who they believe need to submit a tax return. This is based
on information that HMRC held shortly before the end of the
tax year. Random audit cases are provisionally selected from
the population of individuals issued with a notice to file. Der
deadline by which taxpayers must submit their tax return is
31 January the following calendar year (z.B., 31 Januar 2008
für die 2006/2007 tax year). Once returns have been submit-
ted, HMRC deselects some random audit cases (z.B., due to
severe illness or death of the taxpayer). Gleichzeitig,
targeted audits are selected on the basis of the information
provided in self-assessment returns and other intelligence.
Random audits are selected before targeted audits, and indi-
viduals cannot be selected for a targeted audit in the same tax
year as a random audit. The list of taxpayers to be audited is
passed on to local compliance teams who carry out the au-
dits. Up to and including 2006/2007, audits had to be opened
within a year of the 31 January filing deadline, or a year from
the actual date of filing for returns filed late. For tax returns
relating to 2007/2008 oder später, audits had to be opened within
a year of the date when the return was filed. Taxpayers subject
to an audit are informed when it is opened, but they are not
told whether it is a random or targeted audit, in contrast to
work done with U.S. random audits (Long & Schwartz, 1987;
DeBacker et al., 2018). Even after audit, taxpayers are lim-
ited in what they can learn about the audit process because no
details of the programme are made public.3 Approximately
one-third of taxpayers on the list passed on to local compli-

ance teams end up not being audited, largely due to resource
constraints.4

Those who are audited initially receive a letter requesting
information to verify what they have reported. If this does not
provide all the required information, the taxpayer receives a
follow-up phone call, and ultimately in-person visits until the
auditor is satisfied.

Where errors are uncovered, individuals are required to
pay the additional tax due, and interest. If noncompliance
is deemed to be deliberate, the taxpayer might also face an
additional penalty of up to 100% of the value of the underpaid
tax.

B. Data Sources

We exploit data on income tax self-assessment random
audits together with information on income tax returns. Das
combines a number of different HMRC datasets, linked to-
gether on the basis of encrypted taxpayer reference number
and tax year.

Audit records for tax years 1998/1999–2008/2009 come
from Compliance Quality Initiative (CQI), an operational
database that records audits of income tax self-assessment
returns. It includes operational information about the audits,
such as start and end dates, and audit outcomes: ob
noncompliance was found, and the size of any correction,
penalties, and interest.

We track individuals before and after the audit using infor-
mation from tax returns for the years 1998/1999–2011/2012.
This comes from two data sets: SA302 and Valid View. Der
SA302 data set contains information that is sent out to tax-
payers summarising their income and tax liability (the SA302
tax calculation form). It is derived from self-assessment re-
turns, which have been put through a tax calculation process.
It contains information about total income and tax liability as
well as a breakdown into different income sources: employ-
ment earnings, self-employment profits, pensions, und so weiter.
For all of these variables, we uprate to 2012 using the Con-
sumer Prices Index (CPI) to account for inflation, and trim
the top 1% to avoid outliers having an undue impact on the re-
sults.5 We supplement these variables with information from
Valid View, which provides demographics and filing infor-
mation (z.B., filing date). Note that we cannot identify actual
compliance behavior after the audit: the number of random
audit taxpayers that are reaudited is far too small for it to be
possible to focus just on them.

An explicit control group of “held out” individuals was not
constructed at the time of selection for audit. We therefore
draw control individuals from the pool of individuals who
actually filed a tax return (d.h., those who appear in SA302).
This creates some differences in the filing history between
those selected for audit and those who we deem as controls.
In a given year, first-time filers may be issued a notice to file

3Until the publication of this study, even the audit rates were not public

4We address the implications for identification in section IVA.
5In online appendix C.2 we show our results are robust to alternative levels

Information.

of trimming.

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THE DYNAMIC EFFECTS OF TAX AUDITS

549

FIGURE 1.—CHANGE IN THE PROBABILITY OF AUDIT OVER TIME

Constructed using data on individuals who received an audit of their self-assessment tax return for a tax year between 1998/1999 Und 2008/2009, and the full sample of self-assessment returns for the same period.
Quelle: Calculations based on HMRC administrative data sets.

after selection for audit has taken place. They may also end
up back-filing one or two returns. Since we cannot directly
observe the first year in which a notice to file was issued, In
our empirical strategy it is necessary for us to control for the
length of time each taxpayer has been in self-assessment.
More details—including tests to demonstrate this ensures
samples are balanced—are given in section IVA below.

III. Tax Evasion in the UK

In diesem Abschnitt, we first provide some descriptives on the
probability and timeline of audits. We then show that there is
significant noncompliance among individual self-assessment
taxpayers, both in the share of taxpayers who are found
noncompliant and the share of tax that is misreported. More
than one-third of self-assessment taxpayers are found to be
noncompliant, equal to 12% of all income taxpayers.

A. Audit Descriptives

Figur 1 shows the share of individuals per year who face
an income tax random audit over the period 1998/1999–
2008/2009. On average over the period, the probabilities of
being audited are 0.04% (4 In 10,000) for random audits and
2.8% for targeted audits.

Table A1 provides some summary statistics for lags in, Und
durations of, the audit process among random audit cases. Als
described above, up to and including the 2006/2007 return,
HMRC had to begin an audit within 12 months of the 31
January filing deadline; since then, HMRC has had to begin
an audit within 12 months of the filing date. The average lag
between when the tax return was filed and when the random
audit was started is 8.9 months, Aber 10% have a lag of 14
months or more. The average duration of audits is 5.3 months,

TABLE 2.—RANDOM AUDIT OUTCOMES

Proportion of audited returns deemed

Correct
Incorrect but no underpayment
Incorrect with underpayment (noncompliant)

Mean additional tax if noncompliant (£)
Distribution of additional tax if noncompliant

Share £1–100
Share £101–1,000
Share £1,001–10,000
Share £10,001+

Beobachtungen

Mean

Std. dev.

.532
.111
.357
2,314

.116
.483
.361
.039

.499
.314
.479
7,758

.320
.500
.480
.194

34,630

Annual averages for tax years 1998/1999–2008/2009. Includes all individuals with a completed random

audit.

Quelle: Authors’ calculations based on HMRC administrative data sets.

Aber 10% experience a duration of 13 months or more. Taken
together, this means that the average time between a return
being filed and an audit being concluded is 14.3 months, Aber
there are some taxpayers for whom the experience is much
more drawn out: for almost 10% it is two years or more. Das
means that individuals will generally have filed at least one
subsequent tax return before the outcome of the audit is clear,
and some will have filed two tax returns. This will be relevant
for interpreting the results in section IV.

B. Evidence of Noncompliance

We begin by studying the direct results of random audits,
using data on 34,630 completed random audits of individual
self-assessment taxpayers from 1998/1999 Zu 2008/2009.6
Tisch 2 summarises the outcomes of these random audits.
More than half of all returns are found to be correct, 11%

653,400 cases were selected for audit over the period, of which 35,630

were implemented.

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550

THE REVIEW OF ECONOMICS AND STATISTICS

are found to be incorrect but with no underpayment of tax,
Und 36% are “noncompliant,” that is, incorrect and have a
tax underpayment.7 Whilst this is a much higher rate of
noncompliance than has been found in other developed coun-
try contexts, it should be noted that the self-assessment tax
population is a selected subset of all taxpayers. Insbesondere,
it covers those for whom a simple withholding of income at
source is not sufficient to collect the correct tax. This may be
either because some income cannot be withheld (z.B., prop-
erty or self-employed income), or because PAYE struggles
to assign the correct withholding codes (z.B., for people with
multiple sources of pension income). Despite this, since self-
assessment taxpayers make up a third of all UK taxpayers, Das
implies an overall noncompliance rate of 8%–12% among all
taxpayers.8

Turning to the intensive margin, the average additional tax
owed among the noncompliant is £2,314, oder 32% of aver-
age liabilities. Since just over a third of random audits find
evidence of noncompliance, the average additional tax owed
from an audit is then £826.9 However, the distribution is heav-
ily skewed: 60% of noncompliant individuals owe additional
tax of £1,000 or less, whilst 4% owe more than £10,000. In
terms of total revenue, those owing £1,000 or less make up
nur 9% of the underreported revenue; Die 4% owing more
than £10,000 collectively owe more than 42% of the revenue.
Equity concerns around noncompliance are well-known: Es
is seen as unfair that some are not “paying their fair share.”
But this variation in noncompliance is also important for eco-
nomic efficiency. Noncompliant individuals previously acted
as though there was a lower tax rate. This makes their activi-
ties seem relatively more productive than those of compliant
individuals, so it can lead to resource misallocation.

IV. Dynamic Impacts of Audits

In this section we establish two main results. Erste, we show
that audits lead to an increase in reported incomes and taxes in
subsequent years. Looking at total income and total tax, Das
increase lasts five to eight years after the tax year for which
the audit was done. Zweite, we show variation in this impact
by income source. Insbesondere, more autocorrelated income
sources (such as pensions) seem to respond permanently to
audit. Im Gegensatz, income sources that are less autocorre-
verspätet, such as self-employment income, more quickly return

7Incorrect with no underpayment includes those who, Zum Beispiel, owed
no taxes because they had legitimate losses, but had overstated those losses
so would owe less in future years. Anecdotally, it also includes some cases
where actual overpayments of tax were made, although we cannot separately
identify which.

8This is a lower bound, since it assumes everyone who should be in self-
assessment does register, all noncompliance is picked up at audit, and those
who do not need to register are also fully compliant. The range from 8% Zu
12% depends on the assumptions made about the implementation of audits.
Wenn, among those selected for audit, implementation of audit were random,
this would imply a 12% noncompliance rate. Andererseits, if there is
perfect compliance among those for whom audits were not implemented,
this would imply an 8% rate.

9This is the additional tax owed. A further £101 is owed, on average, In
penalties. This is highly concentrated, with less than 7% of those audited
owing any penalty amount.

to baseline. This second result will later help explain why
we see these dynamic responses. Before describing these re-
sults in detail, we first discuss the empirical approach taken.
Briefly, we compare individuals selected for random audit
with those not selected but who could have been selected.
We control for filing history to account for the way the sam-
ple was selected.

A. Estimation

To understand how audits affect future tax receipts, Wir
want to estimate the change in tax paid in the years after
audit that is caused by the audit. We recover this using the
“random audits program” run by the tax authority (HMRC).
This programme selects for audit a random sample of taxpay-
ers from the pool of taxpayers known to be required to file for
a given tax year. One can therefore compare those selected for
audit with others who were not selected but who could have
been.

In each audited tax year we select a sample of individuals
who were not audited and could have been. We assign them
a “placebo audit” for that tax year. We can then compare
them over time to individuals actually selected for audit for
that year. Our sample, daher, consists of individuals who
were selected for random audit in some year between 1999
Und 2009, and individuals who could have been selected in
those same years but were not. Our data on tax returns go
up to 2012. For every individual selected for audit in a given
tax year, we draw six control individuals from the popula-
tion of those who could have been audited in the same tax
year.10

In der Praxis, a little more than two-thirds of those selected
for random audit are actually audited. This is explained by
the high workload faced by the compliance teams implement-
ing audits. Zusätzlich, a small fraction of the control group
(around 2%) is also audited. Random audits are selected be-
fore targeted audits, and no explicit control group was con-
structed to “hold out” some individuals from targeting. To
our knowledge, in prior work only Kleven et al. (2011) have
an explicit control group. This explains why they can only
study a single year after audit—tax authorities are unwilling
to hold off on high-value audits for multiple years. Somit
we compare those selected for a random audit to a “business
as usual” group, rather than a pure control group. This will
tend to reduce the estimated impacts, since individuals in the
control group who are most likely to be noncompliant are
audited.

In the empirical work to follow, we focus on the local av-
erage treatment effect (LATE), instrumenting receipt of audit
with selection for random audit. This is the relevant number
for a tax authority thinking about simultaneously expanding
the size of the random audit programme and the number of
auditors. It gives the average impact h years after audit for an

10In principle, the entire population of taxpayers who could have been
audited could have been used. Jedoch, because the data could be accessed
only in a secure facility at the tax office, computational constraints given
the available hardware limited the sample size that could be used.

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Years after audit

Female

Alter

In London or SE

Has tax agent

Total taxable income

Total tax

Employment

Self-employment

Interest and dividends

Pensions

Property

THE DYNAMIC EFFECTS OF TAX AUDITS

551

TABLE 3.—SAMPLE BALANCE, CONDITIONING ON FILING HISTORY

−5

.274
−.005
.236
49.2
.0
.472
.333
−.003
.159
.628
−.003
.522

−4

Characteristics

.276
−.006
.212
49.3
.0
.600
.334
.001*
.026
.614
−.001
.500

Income and tax totals

35,075
−2
.979
9,646
14
.982

34,670
35
.469
9,539
12
.288

Income components

22,508
11
.758
6,546
56
.298
4,007
−26
.667
3,493
−23
.806
869
−5
.282

22,534
−57
.023
6,379
38
.435
3,905
16
.189
3,542
−23
.482
844
−6
.209

−3

.278
−.005
.292
49.3
.1
.188
.335
.003
.015
.603
−.001
.376

34,030
−163
.012
9,321
−40
.061

22,266
−98
.152
6,200
−49
.033
3,895
−27
.235
3,561
−3
.681
811
0
.525

−2

.282
−.006
.234
49.4
.1
.170
.333
.002
.317
.589
.002
.675

32,912
71
.280
8,979
12
.261

21,708
112*
.049
5,950
−18
.161
3,759
7
.958
3,562
4
.463
769
6
.072

−1

.287
−.005
.338
49.5
.1
.110
.331
.002
.190
.573
.002
.606

31,755
56
.439
8,635
15
.887

21,145
43*
.05
5,581
29
.684
3,645
4
.086
3,531
22
.523
726
0
.518

Mean
Difference
p-value
Mean
Difference
p-value
Mean
Difference
p-value
Mean
Difference
p-value

Mean
Difference
p-value
Mean
Difference
p-value

Mean
Difference
p-value
Mean
Difference
p-value
Mean
Difference
p-value
Mean
Difference
p-value
Mean
Difference
p-value

“Years after audit” measures time relative to audit, or placebo audit for controls. “Mean” is the mean outcome in the control (not selected for audit) group across all years. “Difference” is the coefficient on the
treatment dummy in a regression of the outcome on a treatment dummy and dummies for whether the taxpayer filed taxes in each of the four years before audit (or placebo audit for controls). Treatment dummy equals
1 if taxpayer was selected by HMRC for a random audit. p-values are derived from an F-test that coefficients on interactions between treatment and tax year dummies are all zero in a regression of the outcome of
interest on tax year dummies, interactions between treatment and tax year dummies, and dummies for whether the taxpayer filed taxes in each of the four years before audit (or placebo audit for controls). Das ist ein
stronger test than just testing the coefficient on treatment not interacted. Monetary values are in 2012 Preise. Standard errors are clustered by taxpayer. * P < .05, ** p < .01, and *** p < .001. Source: Authors’ calculations based on HMRC administrative data sets. additional random audit case that might be worked, against which the cost of the audit would be compared. One limitation of our data is a slight mismatch between our treated and control samples in terms of their probability of fil- ing in previous years, for reasons relating to the audit timeline and when they were first issued a notice to file, as described in section IIB. This can be seen in table A2, which docu- ments (unconditional) sample balance between five and one years before audit, for income and tax totals, income compo- nents, and individual characteristics. Overall balancing statis- tics suggest that the samples are fairly well-balanced: the p- value of the likelihood-ratio test of the joint insignificance of all the regressors is 0.181, while the mean and median absolute standardised percentage bias across all outcomes of interest are low at 2.4% and 1.7%, respectively.11 However, 11The standardised percentage bias is the difference in the sample means between treated and control groups as a percentage of the square root of the likelihood of being in the sample in previous years (“sur- vival”) differs between our treatment and control groups. This difference is consistent with how the treatment and control groups were selected, so it might reflect real differences in the samples. We therefore include controls for presence in the data in the years before audit.12 Table 3 shows that once we condition on past survival, the sample is balanced. the average of the sample variances in the treated and control groups (see Rosenbaum & Rubin, 1985). Rubin’s B and R statistics are also well within reasonable thresholds to consider the samples to be balanced, at 10.8 and 0.983, respectively. Rubin’s B is the absolute standardised difference of the means of the linear index of the propensity score in the treated and control group. Rubin’s R is the ratio of treated to control variances of the propensity score index. Rubin (2001) recommends that B be less than 25 and that R be between 0.5 and 2 for the samples to be considered sufficiently balanced. 12In online appendix C.1, we show the results taking a different ap- proach, where we instead use stratified random sampling conditioning the stratification on filing history. Point estimates are similar, and never statisti- cally significantly different from our main approach, although they decline more rapidly from year four. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / / / / 1 0 5 3 5 4 5 2 0 8 9 9 7 9 / r e s t _ a _ 0 1 1 0 1 p d . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 552 THE REVIEW OF ECONOMICS AND STATISTICS FIGURE 2.—DYNAMIC EFFECT OF AUDITS ON TOTAL REPORTED TAX OWED Sample includes individuals selected for a random audit between 1998/1999 and 2008/2009, and control individuals who could have been selected in the same years but were not. It uses tax returns from 1998/1999 to 2011/2012. The solid line plots the point estimate for the difference in average “total reported tax” between individuals who were and weren’t audited, for different numbers of years after the audit. This comes from a regression of total reported tax on dummies for years since audit (or placebo audit for controls), dummies for years since audit (or placebo audit for controls) interacted with treatment status, tax year dummies, and dummies for whether the taxpayer filed a return in each of the four years before audit, with audit status instrumented by selection for audit. Standard errors are clustered at the individual level. Source: Calculations based on HMRC administrative data sets. We therefore estimate the following specification: 8(cid:2) Yihs = αhηh + 8(cid:2) βhηhDi + 2012(cid:2) −1(cid:2) γsTs + δsSis + εihs, h=−5 h=−5 s=1999 s=−4 (1) where Yihs is the outcome for individual i, h years after the tax year selected for audit (with control observations having h = 0 for the tax year for which they were drawn as controls), when the current calendar year is s ≡ t + h. ηh are indicators for being h years after the tax year selected for audit; Di is an indicator for whether the individual is actually audited; Ts is a calendar time indicator for tax year s; and {Si,−1, . . . , Si,−4} are indicators for whether the individual was in the data in each of the four years before audit. The error term, εihs, is clustered at the individual level. Audit status, Di, is instru- mented by (random) selection for audit, Zi. The coefficients of interest are βh ∀h. These estimate the impact of the audit on the outcome variable h years after the tax year selected for audit, measured as the difference in the mean outcome for those actually audited and those who would have been audited only if selected for a random audit. impact on those who were actually audited (i.e., the LATE). The difference in the share audited between the treated and control group is around 66 percentage points, so the LATE is around 1.5 times the intention to treat estimate. The impact of an audit peaks two years after the tax year for which the audit is conducted. This is consistent with the fact that many audits are not started until after the following year’s tax return has already been submitted.13 Reported tax among audited taxpayers is significantly greater than among nonaudited taxpayers for five years after the audit, and the point estimate appears to decline relatively smoothly, getting close to zero by the eighth tax year after the audited year. This pattern of effects is robust to changes in the level of trimming, although, when lower levels of trimming are used, standard errors are larger and consequently some significance levels are lower (see online appendix C.2 for details). From figure 2, we can estimate how much revenue audits raise on average by changing the behavior of audited indi- viduals. Over the five (eight) years after the audited year, the dynamic effects bring in an additional £1,230 (£1,530), 1.5 (1.8) times the direct effect of audit. Although taxpayers in the United States are explicitly told that the random audits B. Overall Impact of Audits Beyond the direct effects of the audit, described in sec- tion II, we also see clear evidence of dynamic effects. Com- paring individuals who were randomly selected for audit with individuals who could have been (but were not) selected, those selected for audit on average report higher levels of tax owed in the years after audit. Figure 2 shows the estimated 13In our sample, almost a quarter of audits are not opened for more than 12 months from the date of filing (see table A1). Additionally, there can be some lag between the tax authority “taking up” a case for audit and notification being received by the taxpayer. If taxpayers each consistently file at the same time every year, this implies at least one-quarter would have filed without knowledge of the audit. More than half will have filed without knowing the result of the audit (table A1). One could instead set h = 0 as the time at which audit begins, but this information is not available for controls, so it risks creating bias if the timing of opening audits among individuals selected for audit is nonrandom. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / / / / 1 0 5 3 5 4 5 2 0 8 9 9 7 9 / r e s t _ a _ 0 1 1 0 1 p d . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 THE DYNAMIC EFFECTS OF TAX AUDITS 553 FIGURE 3.—DYNAMIC EFFECT OF AUDITS ON TOTAL REPORTED INCOME Sample includes individuals selected for a random audit between 1998/1999 and 2008/2009, and control individuals who could have been selected in the same years but were not. It uses tax returns from 1998/1999 to 2011/2012. The solid line plots the point estimate for the difference in average “total reported income” (income from all sources) between individuals who were and weren’t audited, for different numbers of years after the audit. This comes from a regression of total reported income on dummies for years since audit (or placebo audit for controls), dummies for years since audit (or placebo audit for controls) interacted with treatment status, tax year dummies, and dummies for whether the taxpayer filed a return in each of the four years before audit, with audit status instrumented by selection for audit. Standard errors are clustered at the individual level. Source: Calculations based on HMRC administrative data sets. are random, DeBacker et al. (2018) find a similar ratio be- tween direct and indirect effects of audit. Ex ante one might have expected smaller behavioral effects, because taxpayers are aware that the authority is not acting based on any suspi- cion of wrongdoing. Our exploration of the mechanism driv- ing these dynamics will explain why, ex post, these effects should be so similar: the dynamics are driven by constraints to misreporting caused by audit, rather than belief-updating or perceived reaudit risk, both of which may respond to the reasoning behind the audit. These dynamic effects highlight the policy importance of studying the long-term impact of audits: when determining the audit strategy, the revenue-raising effects of audits would be grossly understated without considering the impact on fu- ture behavior. This would imply too few audits taking place. It is important to note that the optimal number of audits will in general not equate the marginal return on audit to the marginal cost of an audit. Audits require real resource costs, while the direct benefits are a transfer of resources from citizens to the state (see Slemrod & Yitzhaki, 1987 for a longer discussion of this point). There are likely also indirect benefits in terms of maintaining overall compliance, as well as potentially intrinsic value placed in upholding the rule of law (Cowell, 1990). Additionally, the social cost of audit must incorporate not only the cost to the tax authority, but also the cost to the taxpayer for which accurate figures are difficult to come by (Burgherr, 2021). We therefore do not attempt a full welfare analysis. Instead we merely note that dynamic effects increase the resources that are transferred to the state without increasing the administrative costs of audit. Assuming that a positive weight is placed on such transfers, taking into account dynamic effects increases the number of audits that should be undertaken. Figure 3 shows that a very similar pattern holds for the im- pact on total income reported. Again there is a clear dynamic effect, peaking two years after the audited year and declin- ing to zero by year eight, though not significantly different from zero by year five. This provides additional support to the previous result for tax, and is not purely by construction, because expenses can often be used to offset income to reduce tax (Carrillo et al., 2017; Slemrod et al., 2017). C. Impact by Income Source We repeat the previous estimation separately by income sources, focusing on income sources for which at least 5% of the sample report nonzero amounts.14 This will be one way in which we discriminate between different possible expla- nations for why we see dynamic effects. Figure 4 shows how the impact of an audit changes over time for the different components of income. Since the mag- nitudes of these incomes are different, for comparability we rescale them relative to the peak impact for that income source. We see that, relative to the peak, self-employment income and dividends decline relatively quickly. Three years later point estimates for these are close to zero, that is, reporting is 14We exclude interest income, because it is very small and not everyone needs to report this, making it hard to compare. See table 1 for information on the share of individuals with each income source. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / / / / 1 0 5 3 5 4 5 2 0 8 9 9 7 9 / r e s t _ a _ 0 1 1 0 1 p d . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 554 THE REVIEW OF ECONOMICS AND STATISTICS FIGURE 4.—RELATIVE DYNAMICS BY INCOME SOURCE: LESS AUTOCORRELATED SOURCES OF INCOME SEE FASTER DECLINES Sample includes individuals selected for a random audit between 1998/1999 and 2008/2009, and control individuals who could have been selected in the same years but were not. It uses tax returns from 1998/1999 to 2011/2012. Each line plots the point estimate for the difference in the average of a particular component of income between individuals who were and weren’t audited, for different numbers of years after the peak impact for that income source. This comes from a regression of each income component on dummies for years since audit (or placebo audit for controls), dummies for years since audit (or placebo audit for controls) interacted with treatment status, tax year dummies, and dummies for whether the taxpayer filed a return in each of the four years before audit, with audit status instrumented by selection for audit. Source: Calculations based on HMRC administrative data sets. TABLE 4.—AUTOCORRELATION BY INCOME SOURCE Corr(t, t − 1) Corr(t, t − 2) Corr(t, t − 3) Pension income Property income Employment income Interest income Self-employment income Dividend income Observations .946 .896 .862 .835 .832 .813 4,506,548 .904 .836 .769 .722 .728 .723 4,506,548 .864 .790 .690 .640 .644 .657 4,506,548 Annual averages for years 1998/1999–2011/2012. Source: Calculations based on HMRC administrative data sets. not different to the control group. In contrast, pension income exhibits little decline. Six years later it retains 80% of the impact, and this is not statistically different from 100%. This pattern is suggestive of the importance of autocorrelation: income sources that one would expect to be more correlated over time appear to show weaker declines. Table 4 shows the autocorrelation for each income source. Pension income is highly autocorrelated because it will typi- cally be an annuity and therefore fixed over time; property in- come is slightly less stable because rents may vary more; and at the other extreme, self-employment and dividend income are considerably less stable. The relative autocorrelations of income sources line up exactly with their speeds of decline.15 There are two caveats to these results. The first is that these measures are noisy, so if confidence intervals were added to 15Note that a comparison of pensions versus property income is helpful in distinguishing this effect of autocorrelation compared with the effect of third-party information. Both have a high autocorrelation, but pension in- come was third-party reported while property income was not. In figure 4 we see essentially the same effect for both sources, despite the large dif- ference in third-party information. Conversely, comparing property income and dividend income—which, like property, is also not third-party reported but has a low autocorrelation—we see very different effects. figure 4 for each income source, many would overlap. The second is that individuals with different income sources may have different propensities for noncompliance. To tackle these concerns, we next use two alternative strate- gies. First, we compare within individuals who have multiple income sources. This immediately solves the second problem above because our results will be within individuals. It will also lead to ten pairwise comparisons: every unordered pair of the five income sources studied. For each pair, our sample is composed of individuals who had both sources sometime in the three years before audit. We then study the relative fall in reporting of each of these income sources four years after the peak. In each case, we expect to find that the less autocorrelated source falls fastest. We find this result in eight out of ten cases. If there were no relationship, we should find this to be true in around five of the tests. The probability of this result under the null of no relationship is 5.5%, close to standard significance thresh- olds. Hence more autocorrelated income sources do seem to decline more slowly than less autocorrelated ones. Our second strategy to tackle concern about heterogene- ity in who receives different income sources is to reweight individuals based on individual characteristics. This ensures that the distribution of observed characteristics is the same across recipients of different incomes. We divide individuals into groups by sex, age band (below 40, 40–65, and above 65—the UK state pension age at which people typically re- tire), and quartiles of filing history. We then run weighted regressions so that the weighted samples match closely the distribution of these characteristics seen among individuals with self-employment income. We replicate figure 4 using the results of the reweighted regression, shown as figure A2. The results look very similar—the only noticeable effects are l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / / / / 1 0 5 3 5 4 5 2 0 8 9 9 7 9 / r e s t _ a _ 0 1 1 0 1 p d . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 THE DYNAMIC EFFECTS OF TAX AUDITS 555 that property income appears to decline slightly faster than previously, and dividend income much faster. Our interpretation for this result, which we formalise be- low, is that audits provide the tax authority with information. Where errors are uncovered, taxpayers file amended returns. Although we do not know, and would not be allowed to reveal, precisely how audit targeting is done, it is clear that “surpris- ing” deviations from recorded historic reports are part of this. The amended return is therefore creating a new benchmark against which future returns will be compared. Hence, income from highly autocorrelated sources will—once uncovered— be hard to hide again, as deviations from the truth will be easily noticed. In contrast, declines in less autocorrelated in- come sources are less informative to the authority because they may well be real for an individual taxpayer. Viewed in aggregate, falls and rises should be equally likely, because the control group will account for any trends in the income source. Hence when we observe a decline in aggregate in- come reports (e.g., for dividend income among audited tax- payers), this can be attributed to noncompliance, although we cannot identify which individuals are the ones underre- porting. Because declines are faster for less autocorrelated income sources, this suggests the importance of information provision. This is something we know to be important from other settings (Kleven et al., 2011; Pomeranz, 2015), although the value of audits as a potential source of information about future tax has not previously been recognised. One caveat to this interpretation is that falls in reporting could alternatively be driven by changes in actual income. For example, those who are audited might sell shares to pay fines, reducing dividend income. Whilst this is possible, it seems unlikely. In cash terms, the peak additional income reported for those who have dividend income is £414. As- suming a high-end estimate for the dividend yield of 10% implies £4,140 of undeclared shares. Conservatively assum- ing also that individuals are on the higher rate of income tax, this implies an additional £135 of tax owed. The abso- lute maximum penalty for misreporting is 100% of the tax due (on top of paying the tax). So selling all these shares (and hence looking like the control group) would be needed only for an individual who is found to have misreported for at least fifteen years, and receives the maximum fine. While such cases might exist, it seems extreme to assume that this is occurring on average. Hence we think it is unlikely that the observed pattern represents changes in real behavior, rather than reporting, though we cannot definitively rule it out. V. Impacts by Audit Outcome We next consider how dynamic effects vary depending on the outcome of audit. This is important for policy, as it helps distinguish whether merely the process of being audited is enough to impact reported income and tax. We find that those who were found to be correct do not respond, while those for whom errors were found increase reported tax. Being audited per se does not appear to increase reported tax—that is, there is no change in behavior among compliant taxpayers—but those found to have underpaid are 18 percentage points more likely to report higher tax owed after audit. We first describe the approach taken to study this question, because our pre- vious control group cannot help us study effects by audit outcome. We then describe the findings highlighted above. A. Empirical Approach Since we now wish to study audit impacts separately by au- dit outcome, we cannot use the earlier identification strategy. In the “placebo audit” group, we cannot observe what audit outcomes would have been, so we cannot construct separate control groups for each audit outcome. Gemmell and Ratto (2012) studied this question by comparing each treatment group to the original control group containing people with a mix of possible outcomes, implicitly assuming that audit out- comes are exogenously assigned. More recently, Beer et al. (2020) used a matched difference-in-difference approach, al- lowing for observable differences in audit outcome. We take an event study approach to answer this question. Our sample for each regression is the set of observations for individuals who are audited and found to have some particular outcome (e.g., found to be compliant). Within that sample, the timing of audit is random—there is nothing systematic that led individuals to be selected in a particular year within the sample. Hence we can compare the outcome for some- one audited and found to have a particular status (e.g., to be compliant) with someone who will be audited and found to have the same status. For our variable of interest, we now focus on a binary variable measuring whether tax paid increases, rather than on the sizes of the increase, as in Pomeranz (2015). In par- ticular, we estimate a linear probability model in which the outcome is whether tax paid in year t is larger than in the year before audit. Our interest now is understanding which individuals—when split by audit status—respond. This out- come is therefore preferred because it compares individuals to their own history, and it is equally responsive to increases for individuals across the distribution of taxes owed. It is also less sensitive to relatively extreme observations, which is more important in our event study approach because the sample size is now much smaller. Whereas previously we had a treatment group of 53,000 individuals, and could draw a large sample of controls from the nonaudit population, now the entire sample is those selected for audit. That sample is then further split into subsamples by audit outcome status, making results more sensitive to outliers and reducing power. Use of a binary variable removes this sensitivity without lim- iting our ability to study which groups respond. In our specification we control for a number of key covari- ates: sex, age, industry, region, and years filing, as well as calendar-year fixed effects. Many of these individual char- acteristics have been shown to be predictive of noncompli- ance (Advani, 2022), so if responsiveness to audit also differs l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / / / / 1 0 5 3 5 4 5 2 0 8 9 9 7 9 / r e s t _ a _ 0 1 1 0 1 p d . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 556 THE REVIEW OF ECONOMICS AND STATISTICS Years since audit Overall −5 −4 −3 −2 −1 0 1 2 3 4 5 Observations −.006 (.013) .007 (.014) .005 (.014) .022 (.014) .056*** (.014) .048*** (.014) .042** (.013) .030* (.014) .031* (.014) .033* (.016) 124,223 Correct −.042* (.018) −.034 (.019) −.023 (.019) −.005 (.019) .016 (.019) .012 (.019) .007 (.020) −.007 (.020) −.0024 (.021) .019 (.023) 46,911 TABLE 5.—IMPACT BY AUDIT OUTCOME Mistake non-positive Mistake positive Positive yield + penalty Not audited .048 (.049) .068 (.049) .058 (.050) .079 (.050) Outcome is difference from −1 so zero by construction .033 (.032) .050 (.033) .039 (.033) .075* (.033) .131* (.051) .109* (.051) .135** (.051) .135** (.052) .134* (.052) .160** (.056) 9,519 .179*** (.033) .174*** (.033) .152*** (.033) .133*** (.034) .137*** (.034) .119** (.037) 25,666 −.014 (.072) .037 (.068) .042 (.068) .032 (.068) .092 (.069) .180** (.069) .207** (.069) .171* (.069) .143* (.070) .128 (.074) 6,983 −.002 (.030) −.006 (.030) −.016 (.030) −.008 (.030) −.014 (.030) −.037 (.030) −.052 (.031) −.048 (.031) −.045 (.031) −.052 (.034) 35,144 The outcome variable is a dummy for whether tax paid is higher in each of the years before/after audit than the year immediately before audit (‘−1’). “Overall” uses the full sample of audited individuals to perform an event study for whether tax paid is higher than in the year before audit. Coefficients from a linear probability model are shown, with standard errors in parentheses. Other columns split the audited sample by audit outcome: tax return found to be correct; tax return found to have a mistake but which doesn’t change tax liability (or in a small number of cases reduced liability); tax return found to have a mistake leading to increased tax liability, but no penalty charged (i.e., treated as legitimate error); tax return found to have underreported liability and a penalty charged (i.e., deemed to be deliberate); tax return selected for audit but no audit actually implemented (placebo test). * p < .05, ** p < .01, and *** p < .001. Source: Authors’ calculations based on HMRC administrative data sets. by these characteristics, then without such controls we may partly pick up a purely compositional effect. B. Results by Audit Outcome To assess the reasonableness of the approach, we begin again by studying the estimated impact in the years before audit. The first four rows of table 5 provide the results for the preaudit period. It can be seen that all the point estimates are close to zero, providing support for the validity of this approach. A second test of validity can be seen from the “Not audited” column. This estimates the effect of being selected for audit on individuals who were never actually audited, nor informed that they had been selected. As expected, again the point estimates are very close to zero. Turning to the other columns, three results can be seen. First, those who were audited and found to have made no errors do not respond. This is important because it tells us that the dynamic response isn’t driven by the mere fact of audit. Direct audit effects could happen, for example, if the process of audit were sufficiently unpleasant that taxpayers decided to err upwards when uncertain in the hope of avoiding further audits. One could also potentially have seen negative direct effects in this group. If some taxpayers were incorrectly found to be compliant, they may learn that the tax authority is less effective at detecting noncompliance than they previ- ously believed, and reduce payments. We find neither of these results: on average, those whose returns are found correct do not change their reports, in contrast to work by Gemmell and Ratto (2012) and Beer et al. (2020). Second, those who are found to have made errors are more likely to report higher levels of tax in subsequent years. Even four years later they are 13–14 percentage points more likely to report higher tax owed. Hence the long-term effects ob- served appear to all come from correcting errors made by the taxpayer. Note that even those who made errors but owed no additional tax respond to the audit. This is because the errors made might affect future tax liability. For example, claiming excessively large expenses today might increase the size of a loss on property income that can be carried forward: cor- recting this increases future tax liabilities. Anecdotally, from speaking to audit officers, in some cases these individuals shift their reports to pay tax in the audit year so that they can smooth out the additional tax liability that they will now face over the coming years. Third, those who receive a penalty appear to have been driving some of the shape of the dynamics we observed ear- lier, where we saw a peak two years after the year selected for audit. Whilst those with mistakes but no penalty respond immediately, the response for those with a penalty peaks two years after the year for which the audit is done. This reflects two features of the audit process. First, those who ultimately receive penalties typically take longest to audit, because their underreporting requires more work to detect. The audit set- tlement date is thus later. If some taxpayers wait until the au- dit (and uncertainty about detection) is resolved to respond, this will delay the time until they are observed to respond. Second, taxpayers with mistakes but no penalties will have their original return corrected, so an immediate response is observed. On the other hand, those who receive a penalty l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / / / / 1 0 5 3 5 4 5 2 0 8 9 9 7 9 / r e s t _ a _ 0 1 1 0 1 p d . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 THE DYNAMIC EFFECTS OF TAX AUDITS 557 may not have their return corrected: in most cases they in- stead file a separate form detailing additional tax, interest, and penalties. Among individual characteristics, the only one which pre- dicts responsiveness overall is sex: women are around 3 per- centage points more likely to respond to an audit. This is purely driven by compositional effects. Judging by audit out- come, there are no differences in responsiveness by sex. VI. Simple Model of Tax Evasion and Audit Response To help understand the mechanism underlying the ob- served results, we consider an extended version of the model of rational tax evasion by Allingham and Sandmo (1972), which is based on the Becker (1968) model of crime. In the Allingham and Sandmo (1972) model, individuals receive income and choose how much to report to the authority. Un- derreporting has the benefit that individuals end up paying less tax, but the cost that they may be caught and receive a punishment on top of paying the correct tax. The probabil- ity of being caught is increasing in the amount of evasion. Kleven et al. (2011) extend this to allow some income to be third-party-reported: underreporting this income is detected with probability 1, so individuals will only evade out of non- third-party reported income. The key innovation of our model is to split non-third-party reported income into more versus less stable sources.16 In- comes from some sources, such as pension annuity income, are very autocorrelated (“stable”), while other sources, such as self-employment income for a sole trader, are much less stable. Autocorrelation captures the extent to which informa- tion learned in an audit today is informative about incomes to- morrow. By first extending the model of Kleven et al. (2011) to multiple time periods, and then allowing for differential autocorrelation of income sources, we are able to distinguish different possible mechanisms for why audits are observed to have long-term effects. Consider an individual who is audited (for the first time) in year t. Being audited may change his/her reporting for some combination of the following three reasons: (i) beliefs about the underlying audit rate or penalty for evasion (“belief up- dating”); (ii) changes in the perceived reaudit risk following audit (“reaudit risk”); and (iii) updates to the information held by the tax authority (“information”).17 In the first of these mechanisms, there is a change in beliefs about fixed parameters, either audit rate or penalty. Conse- quently, any response should also be permanent and common across all income sources. Empirically neither of these is true. Under the second mechanism, the individual perceives a temporary change in the risk of being audited. If s/he per- ceives the risk to have risen, s/he should be more compliant in the short term, but as perceived risk returns to baseline, re- 16Full details and formalisation are provided in online appendix B. 17A formalisation of the following results is provided in online ap- pendix B. porting should do so as well. Conversely, if s/he perceived the risk to have fallen—the so-called “bomb crater effect” (Mit- tone, 2006; Maciejovsky et al., 2007; and Kastlunger et al., 2009)—then s/he should be temporarily less compliant. In both cases, the dynamics of this behavior should be common across income sources. The differential responses across in- come sources, even within individuals, are not consistent with this mechanism. The final mechanism is that audits provide information that differentially changes the ability to hide certain sources of income. Performing an audit provides the tax authority with more accurate information on a taxpayer’s income at a point in time. In subsequent years, information from the au- dit will make evasion of more stable income sources easier to detect, but for less stable income sources the effect will rapidly wear off. Hence under this mechanism, the initial im- pact on reporting behavior will decline back to baseline, and this decline will be more rapid for income sources that have a lower autocorrelation. This is consistent with our findings, as seen in figure 4. VII. Conclusion This paper investigated the dynamic effects of audits on income reported in subsequent tax returns. Understanding these effects is important both from the perspective of quan- tifying the returns to the tax authority from an audit, and for assessing the mechanisms by which audits might influence taxpayer behavior. To answer this question, we exploited a random audit program run by the UK tax authority (HMRC) under which an average of around 4,900 individuals are ran- domly selected for audit each year. We used data on audits over the period 1998/1999–2008/2009, and we tracked re- sponses on tax returns between 1998/1999 and 2011/2012. We established three main results. First, we provided ev- idence of important dynamic effects, with the additional tax revenue over the five years postaudit equalling 1.5 times the direct revenue raised by audit. Second, we documented that a return to misreporting occurred more rapidly after audit for income sources that were less autocorrelated. Third, we showed that only those who were found to have made mis- takes responded to the audit. Extending the standard model of rational tax evasion, we demonstrated that the observed dynamics are consistent only with audits revealing informa- tion to the tax authority, which makes misreporting certain income sources easier to detect for a period after the audit. Our results have three main policy implications. First, tak- ing dynamic effects into account substantially increases the estimated revenue impact of audits. The direct effect of an audit is (on average) £830, whilst the cumulative dynamic effect over the subsequent five years is £1,230, 1.5 times the direct effect. This suggests that the optimal audit rate should be substantially increased relative to the situation in which there are no dynamic effects. A back-of-the-envelope calcu- lation suggests that the cost of an audit to the tax authority is around £2,500, so that even random audits are close to l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / / / / 1 0 5 3 5 4 5 2 0 8 9 9 7 9 / r e s t _ a _ 0 1 1 0 1 p d . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 558 THE REVIEW OF ECONOMICS AND STATISTICS breaking even. For targeted audits, including dynamic effects raises the average return from around £6,000 to £15,000. Second, the variation in dynamic effects observed across different income components alters the way in which tar- geted audits should be targeted: audits should focus more on individuals reporting types of income with the largest overall effects, combining immediate and dynamic effects. For ex- ample, the peak annual impact on reported self-employment income for each self-employed individual is over £1,000— higher than other components. This suggests focusing more on individuals reporting self-employment income. Likewise, although the maximum annual impact on pension income is lower, it is persistent, so there may be more incentive to target individuals believed to be underreporting pension in- come. The precise design of any targeting strategy must of course take into account how taxpayers would respond to the strategy, but for the tax authority the first step in designing any targeting strategy must be to know where the revenue is. Third, there are implications for setting optimal reauditing strategies. Impacts for reported self-employment income and dividend income die away after about four years, so it might make sense to revisit these individuals around this time. In contrast, the impact on reported pension income seems to persist for at least eight years, implying that there is less of a need to reaudit these individuals so soon. Again, the responses of taxpayers to changes in audit strategy must be considered. Our findings also highlight the importance of further study of the indirect effect of tax-compliance audits. One natural direction for further work would be to understand how the dynamic effects vary in the context of targeted audits, which are focused on individuals deemed likely to be noncompliant. A second avenue for exploration is the spillover effect of audits: does auditing taxpayers change the behavior of other taxpayers with whom they interact (Boning et al., 2020)? A third question is the extent to which cheaper “threat letters” can be used to maintain consistently high levels of compliance over the long term in the absence of high audit probabilities. A better understanding of these effects is crucial in determining optimal audit policy. Finally, our results speak to the wider use of audits for pub- lic policy, whether it be to reduce corruption, improve public service delivery, or ensure environmental standards are met. A key lesson is that audits change future behavior but how that behavior changes depends on the likelihood of being caught in the future. Unless there are ongoing incentives to improve compliance—such as increased audit risk, increased penalties, or easier verification of misreporting—changes in reporting may be short-lived. However, a key tradeoff in pub- lic policy contexts is that individuals may be able to dis- continue activities that are subject to audit if the strictness of enforcement is too high. This limits the compliance im- provements achieved (Tulli, 2019), and it may have additional welfare costs as some valuable activities become more expen- sive (Gerardino et al., 2020) or do not take place (Lichand, 2016). Appendices Appendix A Additional Tables and Figures TABLE A1.—RANDOM AUDIT LAGS AND DURATIONS Mean Std. dev. Median 75th 90th Lag to audit start (months) Audit duration (months) Total time to audit end (months) 8.9 5.3 14.3 4.0 6.6 7.3 9 3 13 11 7 17 14 13 23 Annual averages for tax years 1998/1999–2008/2009. Includes all individuals with a completed random audit. Source: Authors’ calculations based on HMRC administrative data sets. TABLE A2.—SAMPLE BALANCE (UNCONDITIONAL) −5 −4 −3 −2 −1 Characteristics Mean .274 Difference −.006 p-value .221 49.2 Mean .2 Difference p-value .756 Mean .333 Difference −.006 p-value .177 .628 .000 .547 .624 .032*** .000 Difference p-value Mean Difference p-value .276 −.004 .359 49.3 .3 .586 .334 .001* .025 .614 .002 .508 .669 .039*** .000 .278 −.002 .606 49.3 .3 .390 .335 .004* .011 .603 .001 .405 .728 .047*** .000 .282 −.001 .627 49.4 .2 .610 .333 .002 .281 .589 .003 .396 .803 .050*** .000 .287 −.002 .863 49.5 .2 .057 .331 .002 .152 .573 .005 .412 .892 .050*** .000 Years after audit Female Age In London or SE Survives Total taxable income Total tax Has tax agent Mean Income and tax totals Mean Difference p-value Mean Difference p-value 35,075 881 .374 9,646 260 .539 34,670 492 .157 9,539 63 .303 Income components 34,030 403* .028 9,321 82 .055 22,266 180* .028 6,200 173 .311 3,895 18 .700 3,561 128 .642 811 37 .576 32,912 1,051* .012 8,979 310 .064 21,708 909** .006 5,950 99 .106 3,759 63 .578 3,562 148 .307 769 47 .498 31,755 1,095* .012 8,635 337* .027 21,145 721* .027 5,581 200* .025 3,645 112 .580 3,531 159 .327 726 31 .134 Employment Self- employment Interest and dividends Pensions Property Mean Difference p-value Mean Difference p-value Mean Difference p-value Mean Difference p-value Mean Difference p-value 22,508 −31 .162 6,546 356 .151 4,007 −36 .767 3,493 176 .425 869 18 .813 22,534 −136 .371 6,379 328 .174 3,905 208 .432 3,542 168 .478 844 −2 .952 “Years after audit” measures time relative to audit, or placebo audit for controls. “Mean” is the mean outcome in the control (not selected for audit) group across all years. “Difference” is the coefficient on the treatment dummy in a regression of the outcome on a treatment dummy. Treatment dummy equals 1 if taxpayer was selected by HMRC for a random audit. p-values are derived from an F-test that coefficients on interactions between treatment and tax year dummies are all zero in a regression of the outcome of interest on tax year dummies and interactions between treatment and tax year dummies. This is a stronger test than just testing the coefficient on treatment not interacted. “Survives” indicates presence in the data. Tests for all outcomes other than “survives” are conditional on survives = 1. Monetary values are in 2012 prices. Standard errors are clustered by taxpayer. * p < .05, ** p < .01, and *** p < .001. Source: Authors’ calculations based on HMRC administrative datasets. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / / / / 1 0 5 3 5 4 5 2 0 8 9 9 7 9 / r e s t _ a _ 0 1 1 0 1 p d . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 THE DYNAMIC EFFECTS OF TAX AUDITS 559 FIGURE A1.—NONCOMPLIANCE OVER THE PRIOR YEAR’S REPORTED INCOME DISTRIBUTION Constructed using data on individuals who received a random audit of their self-assessment tax return for a tax year between 1998/1999 and 2008/2009. Income grouping is done based on previous year’s reported income. A total of 16.2% of individuals report having zero income in the previous year. The remaining individuals are divided into five equal-sized bins based on their previous income: quintiles conditional on reporting nonzero income. “Share of group found to be noncompliant” is the share of individual taxpayers who are found to owe additional tax when audited. “Average additional revenue if noncompliant” is the average total tax in 2012 that was not reported among those individuals for whom some tax was not reported (the noncompliant). “Additional revenue as a share of total tax if noncompliant” is the additional tax owed divided by total tax owed, averaged across individual taxpayers who were noncompliant. Source: Advani (2022). FIGURE A2.—RELATIVE DYNAMICS BY INCOME SOURCE, AFTER REWEIGHTING BY CHARACTERISTICS l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . e d u / r e s t / l a r t i c e - p d f / / / / 1 0 5 3 5 4 5 2 0 8 9 9 7 9 / r e s t _ a _ 0 1 1 0 1 p d . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 Sample includes individuals selected for a random audit between 1998/1999 and 2008/2009, and control individuals who could have been selected in the same years but were not. It uses tax returns from 1998/1999 to 2011/2012. Each line plots the point estimate for the difference in the average of a particular component of income between individuals who were and weren’t audited, for different numbers of years after the peak impact for that income source, after reweighting individuals so that the distribution of observed characteristics matches that seen among the self-employed. This comes from dividing individuals into groups by sex, age band, and quartile of filing history. Observations are reweighted so that the distribution across these discrete cells is the same as for the self-employed. Point estimates for the treatment effect come from a weighted regression of each income component on dummies for years since audit (or placebo audit for controls), dummies for years since audit (or placebo audit for controls) interacted with treatment status, tax year dummies, and dummies for whether the taxpayer filed a return in each of the four years before audit, with audit status instrumented by selection for audit. 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