Geographic Cross-Sectional Fiscal Spending Multipliers: What Have We Learned? — NBER Working Paper 23577
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NBER Working Paper 23577, dated July 2017, is by Gabriel Chodorow-Reich and is titled Geographic Cross-Sectional Fiscal Spending Multipliers: What Have We Learned? The abstract says a geographic cross-sectional fiscal spending multiplier measures the effect of an increase in spending in one region in a monetary union, and that the paper reviews this research and what the evidence implies for national multipliers. Based on an updated analysis of the American Recovery and Reinvestment Act and a survey of empirical studies, the author's preferred point estimate for a cross-sectional output multiplier is 1.8. The abstract says the cross-sectional evidence suggests a national zero lower bound multiplier of about 1.7 or above.
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NBER WORKING PAPER SERIES
GEOGRAPHIC CROSS-SECTIONAL FISCAL SPENDING MULTIPLIERS:
WHAT HAVE WE LEARNED?
Gabriel Chodorow-Reich
Working Paper 23577
http://www.nber.org/papers/w23577
NATIONAL BUREAU OF ECONOMIC RESEARCH
1050 Massachusetts Avenue
Cambridge, MA 02138
July 2017
I acknowledge financial support from The Frank N. Newman Fund in Economics. Disclosure: I
was a staff economist on the Council of Economic Advisers from 2009-2010. The views
expressed herein are those of the author and do not necessarily reflect the views of the National
Bureau of Economic Research.
NBER working papers are circulated for discussion and comment purposes. They have not been
peer-reviewed or been subject to the review by the NBER Board of Directors that accompanies
official NBER publications.
© 2017 by Gabriel Chodorow-Reich. All rights reserved. Short sections of text, not to exceed two
paragraphs, may be quoted without explicit permission provided that full credit, including ©
notice, is given to the source.
Geographic Cross-Sectional Fiscal Spending Multipliers: What Have We Learned?
Gabriel Chodorow-Reich
NBER Working Paper No. 23577
July 2017
JEL No. E62
ABSTRACT
A geographic cross-sectional fiscal spending multiplier measures the effect of an increase in
spending in one region in a monetary union. Empirical studies of such multipliers have
proliferated in recent years. In this paper, I review this research and what the evidence implies for
national multipliers. Based on an updated analysis of the American Recovery and Reinvestment
Act and a survey of empirical studies, my preferred point estimate for a cross-sectional output
multiplier is 1.8. Economic theory of how to map these multipliers into a national multiplier has
also advanced. Drawing on the theoretical literature, the paper discusses conditions under which
the cross-sectional multiplier provides a rough lower bound for a particular national multiplier,
the closed economy zero lower bound multiplier. Putting these elements together, the cross-
sectional evidence suggests a national zero lower bound multiplier of about 1.7 or above, at the
upper end of most studies based on time series evidence. The paper concludes by offering
suggestions for future research on cross-sectional multipliers.
Gabriel Chodorow-Reich
Department of Economics
Harvard University
1805 Littauer Center
Cambridge, MA 02138
and NBER
chodorowreich@fas.harvard.edu
1. Introduction
A geographic cross-sectional fiscal spending multiplier measures the effect of an increase in
spending in one region in a monetary union. The past several years have witnessed a wave
of new research on such multipliers. By definition, estimation uses variation in fiscal policy
across distinct geographic areas in the same calendar period. This approach has a number of
advantages, most notably the potential for much greater variation in policy across space than
over time and variation more plausibly exogenous with respect to the no-intervention paths of
outcome variables. At the same time, cross-sectional multipliers differ in important dimensions
from the national government spending multiplier to which they are often compared. Recog-
nition of these differences has led to pessimism regarding whether cross-sectional multipliers
provide any guidance for the effects of other types of policies.1
In this paper, I assess what we have learned from this research wave. I find the retreat
regarding the literature’s informativeness for other interventions to be premature. Drawing
on theoretical explorations, I argue that the typical empirical cross-sectional multiplier study
provides a rough lower bound for a particular policy-relevant type of national multiplier, the
closed economy, passive monetary policy, deficit-financed multiplier. The lower bound reflects
the high openness of local regions, while the “rough” accounts for the small effects of outside
financing. I then review empirical estimates and find a cross-study mean of about 1.8. Putting
these two elements together, cross-sectional studies imply a larger national multiplier than
1
As part of her review article of fiscal multipliers, Ramey (2011a) concludes: “More research is needed to
understand how these local multipliers translate to aggregate multipliers.” In a more recently published paper,
Fishback and Kachanovskaya (2015, p. 126) write: “The state multipliers cannot be easily translated into a national
multiplier because of spillover effects outside each state’s boundaries and because the same state multiplier can lead
to a broad range of estimates of the national multiplier under a reasonable set of assumptions in a macroeconomic
model.” Many studies include similar caveats.
1
many macroeconomists have assumed.
The paper starts in section 2 by reviewing the econometrics of cross-sectional multipliers.
I discuss a typical approach and compare to the time series literature to highlight the possible
advantages of relying on cross-sectional variation.
Section 3 develops the lower bound argument, following closely theoretical results in Shoag
(2015), Nakamura and Steinsson (2014), and Farhi and Werning (2016). Much of the pessimism
regarding cross-sectional studies arises because in the vast majority of cases, the spending does
not affect the present value of local tax burdens (for example, the spending is paid for by
the federal government). I therefore first consider how the effects of outside-financed spend-
ing compare to local deficit-financed spending. Standard economic theory postulates a small
quantitative difference between the two when the spending is transitory. Intuitively, Ricardian
agents increase their private spending by the annuity value of a transfer, which for transitory
spending implies only a small increase relative to the direct change in government purchases.
Spending by rule-of-thumb, myopic, or liquidity-constrained agents does not depend at all on
the present value of the tax burden; instead, for non-Ricardian agents the comparison to deficit-
financed spending is crucial, since otherwise there is an offsetting decline in output caused by
the contemporaneous higher taxes.
Next, a cross-sectional deficit-financed government spending multiplier differs from a na-
tional multiplier because the cross-sectional multiplier “differences out” other national policy
responses such as a monetary policy reaction and because of the greater openness of local re-
gions. The quantitative importance of the monetary policy reaction for national multipliers
is well known (Woodford, 2011; Christiano et al., 2011). Comparing the local multiplier to a
2
national multiplier when monetary policy does not react, for example because of a zero lower
bound, eliminates this difference between the two multipliers. Greater expenditure switching
and income leakage reduce local multipliers relative to the relevant aggregate multiplier while
greater factor mobility can raise them. Since fixed reallocation costs limit factor mobility in
response to transitory spending changes, the balance of these elements suggests the national
zero lower bound multiplier exceeds the locally-financed local multiplier. Combining these
arguments, in empirically-relevant cases the cross-sectional multiplier provides a rough lower
bound for the closed economy zero lower bound deficit-financed aggregate multiplier.
Sections 4 and 5 review empirical cross-sectional multipliers. In section 4 I provide an
updated example drawn from three papers studying the effects of the 2009 American Recovery
and Reinvestment Act (ARRA). The example illustrates many of the econometric concepts and
provides a template for future studies. I also obtain a number of new results. After applying a
common econometric framework to instruments from each of the three studies, I consistently
find a cost-per-job of the ARRA of roughly $50,000. Using newly available gross state product
data, I estimate an output multiplier of 1.8.
Section 5 reviews the recent empirical literature more broadly. The first part of the section
groups together a set of papers which have examined various components of the ARRA. These
studies all exploit variation homogeneous along the dimensions of the outside nature of the
financing and the short persistence of the intervention, and also all focus on employment rather
than output effects of spending. The cost-per-job across these studies ranges from roughly $25K
to $125K, with around $50K emerging as a preferred number. Using a production function
approach, this magnitude translates loosely into an output multiplier of about 2. The central
3
tendency of these magnitudes closely matches the results from the example in section 4. I then
turn to papers using other sources of variation, many quite creative. The diversity of outcome
variables and policy experiments makes reaching a synthesized conclusion across these studies
harder; nonetheless, those which estimate a cost-per-job find numbers around $30K, and, with
one or two notable exceptions, those which estimate income or output multipliers find numbers
in the range of 1-2.5.
Section 6 summarizes what we have learned. Regarding the informativeness for national
multipliers, after adjusting for spending persistence the mean cross-sectional output multiplier
is 1.8. Applying the rough lower bound result, a cross-sectional multiplier of 1.8 implies a zero
lower bound deficit-financed national multiplier of about 1.7 or above. This magnitude falls at
the very upper end of the range found in a recent review article based mostly on time series
evidence (Ramey, 2011a). Many studies also find higher multipliers in periods and regions
with greater economic slack, pointing to the presence of forces such as lower factor prices or
congested labor markets in generating state-dependent multipliers. I relate these results to
other policy experiments for which cross-sectional studies offer guidance, such as enhanced
fiscal integration in Europe.
Finally, section 7 offer suggestions to help increase the impact of future cross-sectional
multiplier studies, including how to further bridge the gap to the national multiplier.
4
2. Econometrics of Cross-Sectional Multipliers
Consider the relationship:
Dt,t+h Ys = αh,t + βhxs0 Fs,t + γh0 Xs,t + s,t+h , (1)
where Ys is an outcome such as output or employment in geographic area s, Dt,t+h is a difference
operator defined as Dt,t+h Ys = Ys,t+h − Ys,t , αh,t is a time fixed effect, Fs,t is a vector of
components of fiscal policy such as government spending and taxes, and Xs,t is a vector of
covariates.2 The coefficient vector βhxs0 measures the horizon h response of Y to F . The time
fixed effect αh,t in equation (1) characterizes βhxs as a cross-sectional multiplier (xs for cross-
section) because identification of βhxs comes only from variation in fiscal policy across space
within the same calendar period. For the regression estimate β̂hxs to consistently estimate the
true βhxs , there must be variation within a calendar period in Fs,t uncorrelated (conditional
on Xs,t ) with the trajectory of economic activity across areas. This requirement mirrors the
“parallel trends” assumption of difference-in-difference estimation.
2.1. Typical Approach
The typical cross-sectional econometric study starts by identifying some vector of variables
Zs,t which satisfy the conditions for an excluded instrument: Zs,t is correlated with fiscal
policy and the researcher can make an a priori plausible case for the exclusion restriction
E[Zs,t s,t+h |Xs,t ] = 0 ∀h, or in words, that the variables Zs,t are conditionally independent
2
The notation Fs,t is meant to be quite general. For example, the vector could include expectations of future
spending and taxes. Some studies drop the t subscript and implement equation (1) as a pure cross-sectional
regression, while others keep the panel dimension and replace the difference operator on the dependent variable
with an area fixed effect. Because the econometric issues involved with panel fixed effects estimation are similar,
I focus on equation (1) for clarity.
5
of local economic trends.? In some instances, Z,, does not have a monetary representation.
For example, some states have more restrictive balanced budget requirements than others.
Estimation proceeds by instrumenting Fs; with Zs ¢.
Often however Zs; consists of some component of government spending. For example,
suppose federal government spending per capita in state s, G,4, consists of a part constant
across states, G;, a part which responds endogenously to a state’s economy, Get; and a part
Gs which is as-good-as-randomly assigned, where without loss of generality the cross-sectional
means of Goa and Gs are equal to zero. Clearly, the common component G; provides no
variation across states, and by assumption F [Gs.1€s.e+h] # (0. Therefore, a researcher might set
Fy, = Gs4z and Z,4 = Gs. In the first stage regression of a 2SLS estimate (abstracting from
included instruments other than the time fixed effect, i.e. setting X,; to empty),
Gst= TGs 4 + At + Us.t, (2)
the coefficient II has a probability limit of 1 because by assumption of as-good-as-random
assignment EF [(GsrGs.] = 0. With a first stage coefficient of 1, the second stage estimate of
7, is asymptotically equivalent to the reduced form coefficient obtained from simply replacing
F,4 with Z,4 in equation (1). Many studies estimate this reduced form relationship instead of
2SLS. Alternatively, if 7,4 is not independent of the rest of spending F 4 — Zs 4, then the two
approaches will yield different multipliers.4
3Formally, if F’,, is a Kal vector of components of fiscal policy, Zan Mal vector, and X,, an Lal vec-
tor, (i) M > K (order condition), (ii) rank{E[(Z,, Xi)! (FL, X{,)]} = K +L (rank condition), and (iii)
E[Z52€s2+n = 0] Vt, h (exclusion restriction). The last condition is stronger than strictly necessary.
‘If Z,4, the component of spending which satisfies the exclusion restriction, is correlated with the rest of
spending, there may be reason for concern that the variation underlying Z, ; is truly as-good-as-randomly assigned.
In two cases such concern is not warranted. First, other categories of spending may endogenously respond to the
randomly assigned part. Then in the terminology of applied microeconomics, the reduced form coefficient measures
the intent-to-treat and the 2SLS coefficient the effect of the treatment-on-the-treated. Second, the researcher may
Finally, rather than reporting the impulse response function traced by 67°’, many studies
collapse equation (1) into a single regression cumulating the effects across horizons:
= ay + Or" Pst + 9X st +
A
Ds DittnYs
h=0
S- cas ) (3)
h=0
where a, = Sy 9 ane, 8°” = Wig Bry, and yf = 0 Tht: Intuitively, the individual
coefficient 67° gives the impulse response of variable Y at horizon h; summing over these
impulse responses gives the cumulative additional increase in Y. In many instances total
output or total employment per $1 of government spending provides a convenient summary
measure of the multiplier path. Collapsing these effects into a single dependent variable makes
calculations of standard errors straightforward.
2.2. Comparison to Time Series Regression
It is informative to compare equation (1) to a typical time series regression (ts for time
series) used to estimate a fiscal multiplier:
dD t+hY = =at+ Or Fy + 7, Xt + €t+h, (4)
where Y; = )°, Ys, Fi = 02, Fs, and X; is a vector of covariates.
Two main challenges arise in estimating equation (4). First, fiscal policy may adjust in
response to a changing economic trajectory. This reverse causality affects both discretionary
fiscal policy and automatic stabilizers. Researchers must then identify some subset of changes
in F; which are orthogonal to e. Popular approaches include war spending (Barro, 1981;
have identified only a subset of the randomly assigned part of spending. Expanding the example in the text,
let Gop = Gl, +G2,, Zo = Gly, and suppose Corr[G!,,G2,] = p > 0. Then the first stage coefficient
I=1+ n/Van| (G2 ,)/Var(G!,) > 1, the exclusion restriction remains valid, and only the 2SLS coefficient has a
meaningful interpretation.
Ramey and Shapiro, 1998; Hall, 2009), narrative cataloging of policy changes taken for reasons
unrelated to business cycle management (Romer and Romer, 2010), and VAR recursive or sign
restrictions (Blanchard and Perotti, 2002; Mountford and Uhlig, 2009).
The second challenge comes from policy variables which coincide with or respond to changes
in the researcher’s measure of fiscal policy. The response of monetary policy and what happens
to other spending or taxes provide leading examples.5 Thus, an estimate of β ts to exogenous
changes in government spending gives the average effect over the behavior of current and future
monetary policy and taxes in the researcher’s sample and may provide a poor out-of-sample
guide to the effects of government spending under alternative monetary or fiscal regimes.
The cross-sectional approach impacts both of these issues. The time effect αh,t in equa-
tion (1) removes the direct concern of endogenous fiscal response at the highest (e.g. federal)
level. Instead, the researcher need only find a valid reason why Fs,t varies across geographic
areas. Importantly, the time effect does not immediately absolve the researcher of all concerns
of countercyclical federal fiscal policy; targeting of a federal intervention toward geographic ar-
eas more impacted by the recession would violate the requirement that the areas be otherwise
on similar economic trajectories. The time effect also absorbs any monetary policy response or
change in other federal fiscal variables. This consequence of cross-sectional estimation creates
both opportunities and challenges. On the one hand, removing the effect of the endogenous
response of monetary policy or taxes makes the estimate of βhxs more directly tied to primitives
of the economic environment and hence potentially more stable across studies, a point empha-
sized by Nakamura and Steinsson (2014). On the other, it creates some distance between the
5
Theories emphasizing the co-determination of monetary and fiscal policy suggest these two cases are one and
the same (Leeper, 1991). In principle, Ft could include the expected paths of government spending and taxes, but
it rarely does.
8
cross-sectional multiplier βhxs and the more commonly studied aggregate multiplier βhts , an issue
I turn to next.
3. Theory of Cross-sectional Multipliers
The first part of this section relates cross-sectional multipliers to successive policy interven-
tions to provide conditions under which the cross-sectional multiplier provides a lower bound
for a particular type of national multiplier. I then discuss the relationship between output mul-
tipliers and the employment multipliers estimated in many geographic cross-sectional studies.
3.1. Crosswalk from Cross-sectional to National Multiplier
The objective of this section is to develop a relationship between the cross-sectional mul-
tiplier and a judiciously-chosen theoretical construct, the closed economy, zero lower bound,
deficit-financed national multiplier. Many of the concepts discussed arise in the traditional
static Old Keynesian model and its open economy counterpart Mundell-Fleming; others affect
intertemporal budget constraints and arise only in more modern treatments. The discussion
in the text focuses on economic concepts. Online appendix A presents a complete algebraic
model of a cross-sectional multiplier based on Farhi and Werning (2016).6 Shoag (2015) and
Nakamura and Steinsson (2014) also develop many of these points formally.
I start by introducing a convenient theoretical counterpart to βhxs in equation (1). To fix
ideas, consider the following setting. A closed national economy consists of a unit continuum
of local areas which share a common currency. At time t a new path of government spending
6
Relative to that paper, the presentation in online appendix A makes a few functional form assumptions at
the outset and provides sufficient algebraic detail to allow an uninitiated reader to follow along with minimal
interruption.
9
is announced for a single local area s with deviation at horizon h of ∆Gs,t+h . I defer for
the moment discussion of the financing of the new path of spending. The path of government
spending in the rest of the economy remains unchanged. Because area s is infinitesimal, changes
in spending in s do not affect the whole economy. The difference-in-difference in outcomes at
R
horizon h is therefore (Ys,t+h −Ys,t )−(Yt+h −Yt ) = Dt,t+h Ys −Dt,t+h Y where now Yt = s Ys,t ds is
the average value of Y in the economy. Again letting Fs,t denote some measure of the increase in
spending (for example the contemporaneous increase ∆Gs,t or a present value), the counterpart
to equation (1) is:
Dt,t+h Ys − Dt,t+h Y
βhxs = . (5)
Fs,t
I argue that in empirically-relevant cases βhxs provides a lower bound for the effect of in-
creasing spending in the entire economy when monetary policy remains passive. I proceed in
two steps.
3.1.1. Relationship to Deficit-financed Currency Union Spending Multiplier
The multiplier defined in equation (5) has a close relationship to deficit-financed stimulus
policies by individual states or countries operating inside a monetary union. For example,
the consequences of fiscal austerity by members of the euro area has received a great deal
of attention. The possible difference between such policies and the cross-sectional multipliers
reviewed below arises because in the vast majority of cases the spending used to identify
cross-sectional multipliers does not require higher contemporaneous or future local taxes. For
example, when the federal government directs additional highway funds into a particular state,
the tax burden associated with paying for the additional spending falls on residents of all states
10
equally. I refer to such examples as financed by outside transfers, although in practice they
may also involve windfalls generated by other factors such as pension fund abnormal returns.
To understand the difference between multipliers financed by outside transfers and deficit-
financed spending, it helps to further fix some terminology. Let βhxs,transf er denote the cross-
sectional multiplier at horizon h when the spending is financed by external transfers and
βhxs,def icit the cross-sectional multiplier when spending is locally deficit-financed. One can think
of outside-financed spending as comprising an increase in a path of spending which is locally
deficit-financed by issuance at date t of a perpetuity bond and the immediate purchase and
cancellation of the perpetuity by the central government. The present value of the increase
in spending, or equivalently the present value of the transfer from the central government to
R ∞ −rj
cancel the higher debt, is equal to V = 0 e ∆Gs,t+j dj, where r is the real interest rate. Let
βhtransf er denote the multiplier associated with the resources used by the central government to
cancel the locally-issued debt. It follows that:
βhxs,transf er Fs,t = βhxs,def icit Fs,t + βhtransf er V. (6)
I next consider the two cases of an economy inhabited by fully rational agents who can
borrow and lend freely and where Ricardian equivalence holds, and economies dominated by
non-Ricardian agents. In the first, βhtransf er V is small as long as the increase in spending is
transient and the local economy is not too closed. In the second, βhtransf er V can go to zero.
These cases clarify the conditions under which a transfer-financed cross-sectional spending
multiplier closely or exactly resembles a deficit-financed cross-sectional multiplier.
11
When Ricardian equivalence holds. If Ricardian equivalence holds, the wedge between
the outside-financed multiplier and the local deficit-financed multiplier depends on the size of
the transfer, which in turn depends on its persistence, and on the region’s openness. A simple
calculation helps to illustrate. Suppose spending increases by ∆Gs,t on announcement and then
decays exponentially with persistence parameter ρ, ∆Gs,t+j = e−ρj ∆Gs,t , and is financed by
the federal government. Then the present value of the transfer is V = ∆Gs,t × 1/(r + ρ). The
annuity value, equal to the per period interest payment on a perpetuity bond with face value
V , is rV = ∆Gs,t × r/(r + ρ).
In a Ricardian setting where agents obey the permanent income hypothesis and the rate of
pure time discount equals the real interest rate, the partial equilibrium effect of a wealth transfer
on consumption expenditure is equal to the annuity value of the transfer.7 When the transfer
is transient (ρ is large), the annuity value rV is small relative to the increase in government
purchases. The small partial equilibrium response to a transfer to pay for transient spending
transf er
explains why on impact the term βh=0 V can be small in the Ricardian case. Conversely, the
partial equilibrium effect of a permanent increase in outside-financed spending (ρ → 0) is to
immediately raise expenditure by local agents by fully the amount of the increase in government
spending. Openness matters because in general equilibrium the sensitivity of the local output
multiplier depends on whether and how much local residents concentrate their expenditure on
locally-produced output.
The model in online appendix A provides a simple expression combining these elements for
R∞
7
That is, for an agent with intertemporal preferences over consumption c given by Ut = 0 e−rj u(ct+j )dj and a
R ∞ −rj
budget constraint 0 e ct+j dj = W , optimization requires ct+j = rW ∀j. The annuity value is also the required
per period transfer from the federal government to the local region to absolve the local region of ever needing to
raise taxes to pay for the spending.
12
the impact transfer multiplier on local output in a fully intertemporal, Ricardian setting:
l—a r
transfer _ A
where a is the share of purchases from other regions in local expenditure (see equation (A.26)).
Choosing for illustrative purposes a = 1/3, r = 0.03, and p = 0.8 (the last implies about 80%
of the increased spending occurs by date t = 2), the fact that the spending is outside financed
raises local output on impact by only 0.07AG;;. Setting Fs; = AG, in equation (6), in
this example Bestransy —_ reds ‘et | 0 07, a small difference relative to empirical estimates of
Brstransfer discussed below. As prices adjust, the transfer exerts an ever smaller and eventually
negative effect on local output due to a wealth effect on labor supply (see equation (A.35)).
Thus, the impact effect of 0.07 gives the maximum increase in the cross-sectional spending
multiplier due to outside financing at any horizon in this calibrated example.®
Failures of Ricardian equivalence. Failures of Ricardian equivalence can drive 6°!" —
O such that the outside-financed and locally deficit-financed multipliers exactly coincide. The
reason stems crucially from a comparison to deficit-financed rather than tax-financed spending.
For non-Ricardian agents, there is an exact analog between having agents in future periods pay
for current spending and having agents in other areas pay for current spending.
A slight adaptation of a widely-cited counterexample in Ramey (201la, p. 681) sheds
light on the importance of this distinction. In Ramey’s example, all agents have a mechanical
® According to equation (7), the difference between outside-financed and deficit-financed spending multipliers
can become arbitrarily large as the local economy becomes closed. In cashless, intertemporal models the local
region’s current account must balance in present value, so a $1 dollar transfer to local residents in equilibrium
requires local residents to purchase an additional $1 of goods from other regions. If the local economy is quite
closed, it requires a large increase in local consumption to induce any purchases from outside. On the other hand,
the difference vanishes as the economy becomes fully open, since then private spending by local agents does not
fall disproportionately on local products.
13
marginal propensity to consume (mpc) of 0.6 and households in Mississippi receive a government
transfer of $1 financed by a contemporaneous lump sum tax levied on households in other
states. Then, as Ramey points out, the increase in output in Mississippi and hence the local
multiplier equals mpc/(1 − mpc) = 1.5 but the national multiplier is 0.9 The large excess of
the local multiplier over the national multiplier appears to cast doubt on the informativeness
of outside-financed local multipliers. Changing the example slightly, however, suppose instead
that Mississippi financed the transfer by issuing debt purchased by an arbitrarily small measure
of permanent income agents.10 Absent a change in the real interest rate, consumption by
the agents purchasing the debt does not change. Then the local deficit-financed multiplier
also equals 1.5, the same as the outside-financed multiplier and the national deficit-financed
multiplier.
It is informative to move beyond mechanically rule-of-thumb agents to consider three leading
reasons for the failure of Ricardian equivalence. In the first, private agents do not internalize
the prospect of higher future taxes to pay for current spending into their budget constraints due
to life cycle considerations and non-altruistic motives (Weil, 1987). If agents do not incorporate
future tax liability into their private intertemporal budget constraints, then the outside-financed
and locally deficit-financed multipliers coincide. Liquidity constraints provide a second leading
reason Ricardian equivalence may fail.11 If households consume and firms invest based on
current income rather than permanent wealth, then β transf er = 0 and an increase in temporary
9
Following Ramey, this calculation assumes that all consumption is of locally-produced output.
10
The assumption that permanent income agents are the marginal purchasers of debt appears reasonable. Fi-
nancing the spending by imposing lump sum taxes on permanent income agents would of course have the same
effect, but raising taxes only on these agents may be difficult.
11
Evidence for liquidity constraints comes from households’ responses to one-time stimulus payments (Johnson
et al., 2006; Sahm et al., 2012; Parker et al., 2013; Hausman, 2016), from direct examination of households’ liquidity
positions (Lusardi et al., 2011; Kaplan et al., 2014), and from firms’ responses to to temporary cash flows (Fazzari
et al., 1988; House and Shapiro, 2008; Mahon and Zwick, 2015).
14
income resulting from a deficit-financed stimulus package will have equivalent effects to an
outside-financed increase in spending. A third failure stems from myopic or boundedly rational
beliefs (Gabaix, 2015). If agents ignore the intertemporal aspect of their spending problem,
then the outside-financed and locally deficit-financed multipliers again coincide. Similarly, if
agents do not know their region has received an outside transfer, then their private spending
cannot react to the transfer. The low salience case appears plausible in many instances. In the
context of studies of national increases in spending with differential increases across regions,
households would have to know the geographic spending pattern in order to react to any transfer
component.
These examples make clear that in the non-Ricardian case the coincidence result requires
comparing outside-financed spending to a deficit-financed stimulus package. Otherwise, there
is an offsetting decline in private spending from the contemporaneously higher taxes which does
not occur in the outside-financed case.
Quantitative magnitude. How much could the transfer component matter quantitatively?
In models similar to that of online appendix A in which private agents internalize all future
taxes into their budget constraints and calibrated to match approximately the openness and
persistence of government spending in many of the studies reviewed below, Nakamura and
Steinsson (2014, table 8) and Farhi and Werning (2016, table 1) both find outside financing
raises multipliers by less than 0.1, that is, a locally deficit-financed multiplier of 1.2 would
become a multiplier of about 1.25 if outside-financed. This magnitude matches the illustrative
calculation reported above. Intuitively, low persistence of stimulus spending and fairly open
local regions mean that the increase in local purchases of local output in response to the transfer
15
component is small. Farhi and Werning (2016) find this difference remains small even in the
presence of non-Ricardian hand-to-mouth agents as long as the comparison remains to a local
deficit-financed multiplier.
3.1.2. Relationship to Closed Economy Zero Lower Bound Multiplier
Multipliers associated with spending by one entity in a currency union differ from closed
economy multipliers. This section discusses the most important reasons why: absence of
the possibility of a reaction by monetary policy; relative price effects which cause agents to
expenditure-switch toward output produced in other regions; changes in private spending by
local agents fall partly on output produced in other regions; and migration. I conclude that
the balance of these forces likely makes the local deficit-financed multiplier a lower bound for
a particular national multiplier, the closed economy zero lower bound multiplier.
Monetary policy reaction. The first difference – offsetting interest rate changes by monetary
policy makers which reduce the national multiplier – can matter substantially. However, there
exists a leading case when monetary policy does not react to national fiscal policy: at the
zero lower bound. Indeed, determining the national fiscal multiplier when monetary policy is
already constrained is of particular interest to policy-makers. I will call this case the zero lower
bound multiplier.12
Expenditure switching. By purchasing local output, government spending may cause the
price of local output to rise relative to goods produced in other regions. Such price increases
12
The equivalence between the zero lower bound and passive monetary policy is not exact. Monetary policy can
choose not to react to fiscal policy even outside the zero lower bound, while recent experience has revealed tools
(forward guidance, quantitative easing, negative interest rates) available to central banks even after the policy rate
reaches zero. It may therefore be more accurate but less evocative to call this case the “passive monetary policy
multiplier” rather than the “zero lower bound multiplier”.
16
could reflect increases in factor prices, markups, or diminishing returns to scale. As a result of
this terms of trade effect, both local and external consumers and businesses shift expenditure
toward output produced in other regions causing total private purchases of locally-produced
output to fall. This effect makes the cross-sectional multiplier smaller than the closed economy
multiplier. Its magnitude depends on factors such as the nature of price and wage setting, the
degree of segmentation between goods purchased by government and the private sector, and
the substitutability between locally-produced and externally-produced goods.13 I elaborate
briefly here on three elements where future research might contribute to a better quantitative
understanding. Online appendix A provides algebraic detail.
First, the expenditure-switching channel requires that higher government spending cause
local prices to rise. Absence of high frequency, high quality local price measures has made esti-
mating the relative price effect difficult. In the context of spending multipliers, Nakamura and
Steinsson (2014) find no evidence of local consumer prices responding to government spending.
The stability of inflation throughout the Great Recession has also led to some suggestions of
a recent divorce between output and inflation dynamics (Hall, 2011). On the other hand, us-
ing geographic variation in local demand caused by factors other than government spending,
Fitzgerald and Nicolini (2014), Stroebel and Vavra (2016), and Beraja et al. (2016) all find
evidence of local prices responding to local demand conditions.
13
The magnitude does not depend monotonically on the openness of the local region (see equation (A.40) or Farhi
and Werning (2016, p. 2446)). On the one hand, when local agents purchase a large share of their consumption
from local producers, their desire to reduce total consumption when the price of a unit of utility (i.e. the real
interest rate) is temporarily high causes a larger direct reduction in demand from local producers. On the other
hand, this reduction in demand by local purchasers mitigates the rise in the relative price of locally-produced
output, which in turn mitigates the decline in demand from external purchasers. As a result, the increase in the
relative real interest rate emphasized by Nakamura and Steinsson (2014) is not strictly necessary to generate a
reduction in private demand for local goods. In fully open regions with a private sector “home bias” share of zero,
consumption baskets and consumer price indexes of local and external consumers coincide, and hence real interest
rates coincide, but total private demand for local output still falls because of the relative rise in the local producer
price index.
17
Second, by assumption government spending concentrates on goods and services from the
local region; otherwise the cross-sectional multiplier experiment lacks variation in treatment
across regions. Even if the higher government demand for local goods increases their relative
price, this price increase must spillover into goods and services purchased by private agents
to affect their spending. Such spillovers can happen either through competition in output
markets (for example, if government and private agents purchase the same goods), or through
competition in input markets (for example, due to labor mobility across sectors and a common
wage). Segmentation on either dimension will dampen the amount of expenditure switching.
Third, the transmission from relative price changes to expenditure switching depends on
the elasticity of substitution between locally-produced and externally-produced goods. For
temporary government spending shocks, the short-run elasticity is most relevant.
Income effects. The local multiplier also depends on total private spending by local agents,
as any increase in demand “leaks” into other areas. For example, liquidity-constrained workers
whose labor income rises in response to the increase in government spending increase their
consumption of both locally-produced and external goods. Complementarity in the utility
function between consumption and hours worked or excess sensitivity of firm investment to
cash flow would provoke the same effect. This channel is distinct from expenditure switching
because it does not require any change in relative prices to occur. Once again, however, leakage
makes the cross-sectional multiplier a lower bound for the aggregate closed economy multiplier.
The importance of income effects depends on both the rise in purchases by domestic agents
and the openness of the local area. For example, with rigid relative prices and a mechanical
marginal propensity to consume (mpc) and to import (mpm), the local government spending
18
multiplier equals 1/(1−(mpc−mpm)). In most settings, the smaller the local area the larger the
share of purchases from outside the region. Therefore, this effect suggests the cross-sectional
multiplier may increase in the level of the geographic unit, i.e. it is larger for states than
for counties. Recognizing this fact, some cross-sectional studies which examine variation at
a county level enlarge the region covered by the dependent variable to capture some of the
spending leakage.
Migration. In contrast to the expenditure switching and income channels, inward net migra-
tion may push up local multipliers relative to national multipliers. As local government spend-
ing causes local labor demand to rise, workers may move in from other areas. The population
influx further raises local employment and output as the immigrants consume non-tradeable
output and push down wages in tradeable sectors.
Because of fixed costs of moving, the importance of the migration channel rises with the
persistence of the spending. Likely for this reason, none of Farhi and Werning (2016), Shoag
(2015), or Nakamura and Steinsson (2014) allows for net migration in their theoretical model of
cross-sectional multipliers. In contrast, studies of longer run changes or more persistent policies
treat population spatial equilibrium as a key force.14 With fixed costs the importance of the
migration channel also depends on the size of the local geographic unit, as migration of workers
across neighboring counties engenders smaller costs than migration across states. Shoag (2015)
14
See e.g. Moretti (2010) for analysis of long-run employment multipliers and Glaeser and Gottlieb (2008) for
a formal spatial equilibrium model. Moretti (2010) estimates the additional aggregate local employment caused
by an additional job in different sectors, at decadal frequency. Assuming that immigration makes the local labor
supply elasticity larger than the national, he argues that the employment multiplier of an additional job in a
non-traded sector provides an upper bound of the national spending multiplier and the multiplier of an additional
job in a traded sector provides a lower bound. This argument also implicitly assumes changes persistent enough
to induce migration and that output and employment are not demand-constrained. While possibly reasonable
assumptions for the decadal frequency Moretti examines, failure of these assumptions at shorter horizons make
the bounds inapplicable to short-run spending multipliers.
19
and Nakamura and Steinsson (2014) each estimate the cross-state population response to local
government spending and find economically and statistically insignificant responses. Thus, for
temporary increases in local government spending, the empirical relevance of the migration
channel appears small.
Other channels. Other potential differences between local currency union and national mul-
tipliers are hard to quantify or even sign. Confidence provides one example. By passing
a countercyclical fiscal stimulus, a national government might raise consumer and business
confidence in the government’s competence or more nebulously trigger “animal spirits”. Alter-
natively, if private agents view the spending as an insufficient response to the circumstances
or contaminated by political favoritism, confidence might fall. Looking further ahead, the
political reaction to national spending might affect outcomes of future elections and hence a
host of other policies. Because these channels have ambiguous sign and vary with specific
circumstances, they resist incorporation into a general framework. Put differently, local multi-
pliers can inform only about a national multiplier for which channels such as confidence in the
national government do not play a role.
3.1.3. Summary and discussion
As described in section 3.1.1, multipliers for transitory increases in local spending not
financed locally map roughly into locally deficit-financed currency union multipliers. Sec-
tion 3.1.2 argued that locally-financed currency union spending multipliers provide a lower
bound for closed economy zero lower bound multipliers due to the dominance of the expenditure-
switching and leakage effects. Combining these two results, standard theory suggests that in
empirically-relevant cases cross-sectional multipliers provide a rough lower bound for deficit-
20
financed zero lower bound closed economy multipliers. While shared by Nakamura and Steins-
son (2014) and Farhi and Werning (2016), this conclusion is sharply at odds with much of the
conventional wisdom extant at the start of this wave of research.15
I conclude this section with a brief discussion of issues related to the size of the local region
and the openness of the national economy. The assumption that spending occurs in a single
area s of infinitesimal size highlights an important difference between the issues which affect
the mapping from βhxs to βhts and the no-interference stable unit treatment value assumption
(SUTVA) often made in analyses of clinical trials and other randomized experiments. SUTVA
states the condition that for the difference between treated and untreated units to provide a
valid estimate of the causal effect of treatment, treatment of one unit must not affect outcomes of
the non-treated units. When s is infinitesimal the spillovers from higher local spending, arising
inter alia from expenditure switching, income effects, and migration, are infinitesimal relative
to the rest of the economy and SUTVA holds. Nonetheless, the local multiplier estimated
from the difference in outcomes between the single region s and the whole economy may differ
from the effects of spending in the entire economy because economic integration has first order
effects on outcomes in s.16 This discussion makes clear two additional issues. First, when s is
15
For example, Giavazzi (2012, p. 144) writes that “local multipliers deliver an upward biased estimate of
total spending multipliers” (emphasis mine), echoing the example from Ramey (2011a) discussed above. A recent
literature has questioned the plausibility of some of the forward-looking elements of the New Keynesian model
which give rise to potentially very large closed economy zero lower bound multipliers (McKay et al., 2016; Kaplan
et al., 2016). The rough lower bound result does not depend on these particular features. Indeed, aspects which
make the New Keynesian model less forward-looking also rule out one case discussed by Farhi and Werning (2016)
in which closed economy zero lower bound deficit-financed spending may generate a contemporaneous multiplier
of less than the locally-financed currency union multiplier, wherein the presence of liquidity constrained agents
results in expectations of a recession in the future at the time taxes rise, thereby generating in the closed economy
case a deflationary spiral which reduces current expenditure by unconstrained agents. Enough price rigidity also
rules out this outcome.
16
Formally, suppose the national economy has population normalized to 1 and consists of N equally sized regions.
The effects of economic integration on the local region s and the rest of the economy are both of order 1/N . As
N → ∞, the effect of spending in s on the national economy vanishes but the effect on the local region remains
of the same order of magnitude as the region’s size, 1/N . Note also that while related empirically, the concepts
of region size and openness are theoretically distinct; a region of size 1/N may sell an arbitrary fraction α of its
21
not infinitesimal SUTVA will not hold and βhxs measures the effects of spending on outcomes
in s relative to the effects in other areas. Thus, if the cross-sectional multiplier based on
spending in one local area understates the national zero lower bound multiplier, the cross-
sectional multiplier based on increasing spending in a randomly chosen half of all U.S. states
would further understate the national multiplier. In practice, however, most studies consider
sufficiently small geographic units that the infinitesimal assumption likely provides a reasonable
approximation. Second, while adding spending in other areas to equation (1) can potentially
incorporate some of the spillovers, it does not turn βhxs into a national multiplier.
What if the national economy is not closed? Openness of the national economy does not
affect the local multiplier when s is infinitesimal because the national economy does not respond
to changes in s. However, as international macroeconomists have known since Mundell (1963)
and Fleming (1962), national multipliers do depend on the openness of the national economy
for reasons similar to those discussed in section 3.1.2. The comparison to a closed economy
multiplier simply reflects the absence of information from a cross-sectional multiplier for the
difference between the multiplier in national closed versus open economies.
3.2. Relationship Between Employment and Spending Multipliers
While national multipliers typically take the form of dollars of GDP per dollar of spending,
at the U.S. state level the Bureau of Economic Analysis only began in December 2015 to
publish real gross state product (GSP) at a quarterly frequency and measures of output at
the county level remain in development. In contrast, the Bureau of Labor Statistics reports
monthly employment by state or county based on high quality administrative data from the
output to other regions.
22
unemployment insurance system. The availability of high quality employment but not output
data at a local level holds true in many other countries as well. For this reason, many geographic
cross-sectional studies calculate employment rather than output multipliers. Here I derive a
mapping between the two.
Let βhY denote the output multiplier and βhE the employment spending multiplier. That is,
for a deviation in spending of ∆Gt , by definition:
∆Yt+h = βhY ∆Gt ,
∆Et+h = βhE ∆Gt ,
where Yt is GDP, Et is employment, Gt is government spending, ∆ denotes the deviation from
some baseline path, and I drop the geographic subscript for simplicity. Let et+h = ∆Et+h /Et
denote the percent change in employment caused by the spending, yt+h = ∆Yt+h /Yt the percent
change in output, and gt = ∆Gt /Yt the deviation of spending as a share of output. It will be
useful to write:
Yt
et+h = βhE gt .
Et
I assume a production function relating outputs and inputs Yt = A (Ht Et )1−ξ , where Ht
denotes hours per worker. Implicitly, this functional form assumes capital does not adjust in
the short run. Let ht = ∆Ht+h /Ht . Then:
yt+h yt+h et+h Yt
βhY = = ≈ (1 − ξ) (1 + χ) βhE , (8)
gt et+h gt Et
where χ = ht /et denotes the elasticity of hours per worker to total employment. For the United
23
States, ξ ≈ 1/3 and χ ≈ 0.5, yielding a combined multiplicative factor of (1 − ξ) (1 + χ) ≈
1.17 As an alternative, Nakamura and Steinsson (2014) report estimates of both β Y and
the combined factor β E × Y /E, the latter being the coefficient from a regression of et on gt .
Reassuringly, the ratio of these two estimates is close to unity. Therefore, for the United States
a rough translation from employment to output multipliers is to divide output per worker Y /E
by the cost-per-job 1/β E , taking care to make sure that Y /E and β E correspond to the same
calendar length of time.
4. Example of a Cross-Sectional Multiplier
I illustrate the cross-sectional approach by presenting a unified set of results based on cross-
state variation generated by the American Recovery and Reinvestment Act (ARRA). Enacted
in February 2009, the ARRA included new spending, transfers, and tax reductions totaling
roughly $800 billion. As legislation proposed by the incoming president with the explicit intent
of mitigating the recession already underway, the ARRA offers little useful time series variation
for assessing the consequences of fiscal policy.18 Instead, researchers have identified aspects of
the spending allocation which resulted in geographic variation plausibly exogenous to economic
trends. Crucially, more than half of the budgetary outlays went either to contractors directly
or to subnational governments, and an unusual provision of the bill, section 1512, tracked such
spending by requiring federal agencies to report outlays in each state and all prime recipients
to report the funds received. The combination of the variation in geographic entitlement in
17
The estimate of ξ = 1/3 based on factor income shares is standard. Okun (1962) provides an early estimate
of the relative movement of hours per worker and employment and Elsby et al. (2010) an updated estimate.
18
A few papers have used historical time series patterns to study the ARRA (Romer and Bernstein, 2009; Cogan
and Taylor, 2012; Carlino and Inman, 2014).
24
many of the act’s programs and the detailed data collection facilitated research efforts.
4.1. Econometric Choices
IT implement equation (3) as a purely cross-sectional 2SLS regression:
=at BF, +7 X54 6s, (9)
A
S/ (Ystrn — Ys)
h=0
Fo =U) +7, + 5X, + vs, (10)
where Y, is either annualized employment (normalized by the adult population) or gross state
product (GSP):
yemp. emp. _ 1 Employment, +p, _ Employment, ,
s,tth s,t a 12 Working age population, ;
GSP — GSP
GSP GSP s,tth 8,t
Yotth — Y, t = GSP. :
I set t, the start of the treatment period, to December 2008. As emphasized by Ramey (2011b),
agents may start responding to a fiscal shock at the moment of announcement and estimates of
multipliers should incorporate these anticipation effects. Chodorow-Reich et al. (2012) argue
that important components of the ARRA were already apparent in that month. Roughly three
quarters of the total ARRA had been outlaid by December 2010, with the remainder spread
over a number of years. The endogenous variable F’ is therefore total ARRA outlays through
2010M12 and is expressed either as a ratio to the adult population or to GSP to match the
normalization of the dependent variable. I set H to 24 months to match the duration over
which I measure spending. Thus, equation (9) measures the effect of $1 of outlays on either
cumulative output or cumulative employment, with the latter expressed in terms of the number
25
of “job-years” by dividing the summation of additional monthly employment by 12.
I consider three measures of Zs,t used in prior studies. Each follows the logic that allocating
$800 billion in a short legislative timespan required Congress to use some existing spending
formulas which did not particularly target areas hardest hit by the recession. The first comes
from Chodorow-Reich et al. (2012). Roughly $90 billion of federal aid to state governments
came in the form of an increase in the federal share of Medicaid expenditure (the FMAP),
effectively giving larger grants to states with higher secular per capita Medicaid spending.
Because the increase in the FMAP also depended on the state’s unemployment rate, which is
clearly endogenous to the economic trajectory, Chodorow-Reich et al. (2012) use pre-recession
Medicaid spending as an instrument for the FMAP transfer component. The second proposed
Zs,t comes from Wilson (2012) and Conley and Dupor (2013) who note that the distribution
of $27 billion of highway construction spending depended on pre-recession formulas using as
inputs total lane miles of federal highway, total vehicle miles traveled on federal highways,
tax payments paid into the federal highway trust fund, and Federal Highway Administration
obligation limitations. I follow Wilson (2012) and use a linear combination of these four factors
as an instrument for Department of Transportation spending. Dupor and Mehkari (2016)
take the idea of identifying spending allocated according to pre-recession formulas to its logical
extreme and aggregate all components of the ARRA which fit this description. The components
identified by Dupor and Mehkari (2016) constitute the third proposed Zs,t .19 I normalize each
Zs,t by either the adult population or GSP to match the normalization of the dependent variable.
19
The Dupor and Mehkari (2016) use of local recipient reporting means that their list of programs excludes the
FMAP increase and the highway spending. I make the following changes to the instruments used in these papers.
For Wilson (2012), I update the projection of ARRA highway obligations on the four formulaic components to
include obligations in 2010. For Dupor and Mehkari (2016), I use the agency-reported spending in their identified
programs rather than the spending as reported by recipients.
26
I include three measures of economic conditions in Xs : the employment change from
2007M 12 to 2008M 12, the growth rate of GSP from 2007Q4 to 2008Q4, and the 2008M 12
employment level, where the employment variables are normalized by dividing by the 2008M 12
adult population.20 A good control variable should correlate either with the outcome variable
(“economic trajectory” controls) or the instrument (“exclusion restriction” controls), where of
course these sets may overlap. In this case, controlling for pre-treatment trends both reduces
standard errors by absorbing residual variation in the dependent variable and weakens the ex-
clusion restriction by making the as-good-as-random assignment conditional on the pre-existing
economic conditions. Nonetheless, with 50 observations and many seemingly sensible control
variables, the choice of covariates can matter quantitatively. Such sensitivity may just reflect
in-sample over-fitting or less innocuously suggest a violation of the exclusion restriction. Each
of Chodorow-Reich et al. (2012), Wilson (2012), and Dupor and Mehkari (2016) contains a
more exhaustive set of control variables than used here. I augment Xs,t with some of these
controls in online appendix B and find the results reported below do not change much. Such
sensitivity analysis is common in the cross-sectional multiplier literature and an example of how
readily the many tools developed in applied microeconomics for validating research designs can
be imported (see Athey and Imbens, 2017, for a recent survey).
4.2. Results
Table 1 reports the results. Columns (1)-(3) report the second stage coefficient for the
employment multiplier using each instrument separately. While the correlation coefficient be-
20
The employment data come from the Bureau of Labor Statistics Current Employment Statistics, an
establishment-based count of payroll jobs based (after annual benchmarking) on monthly administrative counts
of employees covered by the unemployment insurance program. I translate all employment variables into per
capita by dividing by the civilian non-institutional population 16+ in 2008M 12 as reported in the BLS Local Area
Unemployment Statistics.
27
Table 1: ARRA Example
Dependent variable:
Job years per $100K spent GSP
(1) (2) (3) (4) (5)
Endogenous variable:
Total ARRA spending 2.15 2.06 1.83 1.99 1.76
(0.65) (1.16) (0.66) (0.55) (1.26)
Instruments FMAP DOT DM ALL ALL
Estimator 2sls 2sls 2sls 2sls 2sls
First stage coefficient 0.38 1.78 6.71 . .
First stage F statistic 41.2 11.4 50.4 59.4 151.8
First stage R2 0.48 0.29 0.57 0.80 0.89
Hansen J statistic p-value 0.88 0.36
Observations 50 50 50 50 50
Notes: The table reports cross-state regressions of the effect of ARRA spending on employment (columns 1-4)
or gross state product (column 5) during 2009 and 2010. ARRA spending is instrumented using pre-recession
Medicaid spending (FMAP), Department of Transportation formula (DOT), and other pre-recession forumlae
(DM) as described in the text. All specifications also control for the employment change from December 2007
to December 2008 normalized by the December 2008 population 16+, gross state product (GSP) growth from
the fourth quarter of 2007 to the fourth quarter of 2008, and the December 2008 ratio of employment to the
population 16+. In columns (1)-(4) Total ARRA spending and the instruments are normalized by the December
2008 population 16+. In column (5), Total ARRA spending and the instruments are normalized by 2008Q4 GSP.
Eicker-White standard errors in parentheses. Following AEA guidelines, symbolic indicators of significance are
omitted.
tween the DOT and DM instruments is fairly high (0.74), perhaps explaining the large first
stage coefficients in columns (2) and (3), neither variable is highly correlated with the FMAP
instrument (0.04 for DOT and 0.14 for DM).21 Nonetheless, the estimated employment effect
is remarkably stable across columns. Column (4) groups the instruments together. The co-
efficient of 1.99 has the interpretation of an additional $100K of ARRA spending in a state
increases employment by the equivalent of 1.99 jobs each of which lasts for one year, or a “cost-
$100K
per-job” of 1.99 jobs = $50, 250. Using the delta method, the 90% confidence interval for the
“cost-per-job” is ($27,500,$73,250). The first stage R2 rises substantially in column (4) and the
21
The first stage coefficient in column (1) should differ from one because the FMAP increased by 6.2 p.p. and
because Medicaid spending in 2009 and 2010 was higher than Medicaid spending in 2007.
28
second stage standard error falls, indicating improved efficiency by combining the instruments
together. The J statistic fails to reject exogeneity.
Column (5) uses the newly available gross state product (GSP) data to estimate an output
multiplier of 1.76, although with less precision than the employment results.22 To compare the
employment multiplier estimate in column (4) to the GSP multiplier in column (5) I use the
approach outlined in section 3.2. Output per worker Y /E in the national income accounts was
$105K in 2009. Applying this number to the cost-per-job estimated in column (4) yields an
implied output multiplier of around two, reassuringly close to the direct estimate of the output
multiplier of 1.76 in column (5).
4.3. Interpretation
To relate the multipliers in table 1 to the outside-financed spending multiplier studied in
section 3.1 I return to two issues raised above and which recur in many of the studies reviewed
next. The first concerns the timing of the employment and output effects. The multiplier
obtained from estimating equation (9) characterizes the cumulative effect on employment or
output over H periods. If the impulse response of Y remains non-zero past H periods, βh 6= 0
for h > H, then extending the horizon would change the multiplier. Plotting the impulse
response coefficients can help to assess the sufficiency of truncating the response at H periods
and I do so in figure B.1 for the employment response for 0 to 48 months. In this case,
22
In column (5) I normalize the endogenous variable and the instruments by the level of GSP in 2008Q4 such
that the coefficient on Total ARRA spending has the interpretation of a dollar-for-dollar multiplier. The degree
of measurement error in real GSP data – especially as compared to state employment data which derive from
administrative tax records – may explain the larger standard error for the output multiplier. The methodology
underlying the real GSP data further invites caution in their use for studying multipliers. For example, their
construction does not allow for a local price response to increased government purchases (Cao et al., 2016), an
issue of potential importance as discussed above. Appendix table B.1 reproduces the estimates shown in table 1
along with the coefficients and standard errors for the included covariates.
29
the coefficients remain positive past the 24 month horizon. A complication arises, however,
because of additional stimulus enacted after the ARRA. According to Council of Economic
Advisers (2014, p.101), such measures accounted for an additional $709 billion in spending,
transfers, or tax reductions, or nearly the magnitude of the initial ARRA, with the vast majority
coming in 2011 and 2012. Importantly, some of these measures directly extended components
of the instruments used in table 1. Because legislative passage of the additional measures
occurred only in late 2010 or after, they had limited impact on employment or output through
2010. Interpreting the table 1 multipliers as capturing the infinite horizon employment effects,
however, here requires an assumption that the effects past month 24 stem solely from post-
ARRA spending.
The second issue concerns the choice of endogenous variable Fs . Equation (9) follows much
of the literature and uses total ARRA outlays. Yet, even if some states received more ARRA
outlays for essentially random reasons, total government purchases in those states need not
have increased dollar-for-dollar with the ARRA component. States could instead have used
federal transfers to reduce taxes or increase balances in their rainy day funds. Even direct
federal purchases (as used in some of the studies reviewed below) can crowd out or in state and
local spending. Data on state and local finances can distinguish among these possibilities.23
In appendix table B.3, I use these data to estimate that an additional $1 of ARRA transfers
during 2009 or 2010 increases state and local expenditure by a total of $1.21 (s.e.=0.63) during
FY2009 and FY2010 and reduces taxes by $0.16 (s.e.=0.37). The near dollar-for-dollar increase
in expenditure and small effect on taxes imply the multiplier in table 1 approximates the local
23
Unfortunately, publication of such data by the Census Bureau occurs with a multi-year lag with the conse-
quence that many studies do not make use of them. Leduc and Wilson (2017) is an important exception and finds
crowding in of ARRA highway grants.
30
outside-financed spending multiplier.
5. Summary of Empirical Cross-sectional Multipliers
I now review recent empirical studies of geographic cross-sectional multipliers.24
5.1. Evidence from the ARRA
Because studies based on the geographic distribution of funds under the 2009 ARRA all cover
roughly the same time period and intervention, I treat them as a separate group. Importantly
from the lens of the theoretical discussion, these studies all involve fiscal transfers of the same
persistence, the approximately two year time frame of payouts from the bill.
Table 2 summarizes the results from these papers. As a concise summary measure, the
final column reports the number of job-years associated with an additional $100K of ARRA
spending implied by each study. Where possible, I report the 90% confidence interval for this
number in brackets.
The largest cross-state estimated employment effects come from the Chodorow-Reich et al.
(2012) study of aid to state governments through the Medicaid matching program described
in section 4. Two aspects of the program may have led to high employment multipliers. First,
fungible aid allows state governments to direct the funds to their best use. Chodorow-Reich
et al. (2012) report a concentration of effects in reduced layoffs of workers in sectors funded
by state and local government. Second, states began receiving money under this program
24
A closely related literature and one that predates many of the papers reviewed here studies the direct effect of
various fiscal stimulus policies using some cross-sectional variation in the eligibility or timing of the policy at the
level of the individual recipient. See e.g. Johnson et al. (2006); House and Shapiro (2008); Parker et al. (2013);
Mian and Sufi (2012); Hausman (2016); Mahon and Zwick (2015). Unlike geographic cross-sectional multipliers,
these studies contain no general equilibrium effects and thus pose a distinct challenge for mapping to a national
multiplier. Davis et al. (1997) and Hooker and Knetter (1997) are examples of earlier papers which estimate a
specification similar to equation (1). Zidar (2017) estimates a similar specification for tax changes.
31
Table 2: ARRA Papers
Study/ Jour-
nal
Identification
Geography
Headline Result
Job-years per
$100K
Chodorow-Reich
Pre-recession Medicaid
$100K increases employment by 3.8
et al. (2012), spending instruments state State . 3.8 [1.2,6.4].
AEJ:Policy fiscal relief [1.2,6.4] job-years
Conle and ARRA highway obligations $100K increases employment by 0.5
Du i (2013) and state tax revenue cycli- [(0.05,0.94] job-years if fungibility
Journal of Mon. cality instrument ARRA _ State between ARRA and lost tax rev- 0.76 [-0.1,1.64].*
; spending net of change in enue imposed; 0.76 [-0.1,1.64] job-
etary Economics § 8 J
tax revenue years if fungibility not imposed.
$100K increases employment in
County-level fixed effects own county by 0.76 [0.39,1.12] job-
Dube etal. re nescion with statex-vear years and in all counties within 120
(2014), Unpub- fecal effects and Beatikondl County miles of county by 3.28 [1.73,4.83] 3.28 [1.73,4.83].°
lished demoeraphic control job-years. Employment. effects
Mograpme COnsTors larger in counties with greater ex-
cess capacity.
$100K increases employment
Dupor and Formulaic Recovery Act Subregional by 1.03 (0.39,1.66] | and 0.85
McCrory . spillovers [(0.39,1.31] job-years in own and
spending by federal agen-
(Forthcom- cies not tareeted to hard within lo- neighboring subregion jobs, re 1.85.°
ing), Economic hi . " io Tee reer cal labor spectively, and increases wages
Journal Hb TegIONS markets by $64K [$28K,$100K] and $50K
[$22K ,$78K], respectively.
Dupor and Formulaic Recovery Act .
. . $100K increases employment by
pean es Boe £8E8 bill by $102K [$48K,$156K].
nomic Review hit regions
Fevrer and Sac- Mean seniority of a state’s $100K increases employment
onlote (2012) Congressional delegations State by 2.16 [0.99,3.33] (IV) or 0.93 1.99 [0.78,3.21].4
Unpublished * instruments ARRA spend- [(0.42,1.44] (OLS) jobs in October ~~ coe
P ing 2010.
os er een $100K of funding announcements
Se inarts of i hwa increases employment in February
Wilson (2012), . _eaway 2010 by 0.81 [0.23,1.39] jobs; $100K
. spending allocation, and State . peer 1.75 [0.58,2.9].°
AEJ:Policy schoolin ave opula- of funding obligations increases em-
tion wetrent PRR A ployment in February 2010 by 1.02
spending [(0.43,1.61] jobs.
Notes: a. Fungibility not imposed specification.
b. Based on specification including spillovers.
c. Summing direct and spillover effects. The covariance between the two is not reported.
d. Feyrer and Sacerdote (2012) baseline IV regression re-estimated with the dependent variable Y, =
12 t=2009M3
Population,
Populationggog yo
1 2010M10 (Sere _ Employmentyo99 72
[0.42,1.53].
) . The corresponding range for the OLS specification is 0.98
e. Wilson (2012) baseline regression re-estimated with the right hand side variable outlays through March
2011 and the dependent variable Y, = +
12 24.t=2009M3
32
2011M3 Employment, — Employmentaoo9 a2
Population, .
Populationggg9 yz2
immediately after the bill’s passage, in contrast to other programs such as highway construction
reimbursements most of which came one to two years later. Thus, states received the Medicaid
matching transfers exactly when state budget shortfalls first materialized. On the other hand,
the employment multiplier estimated in Chodorow-Reich et al. (2012) exceeds that in column
(1) of table 1 using similar variation but a slightly different specification.25 Dupor (2013)
emphasizes the importance of keeping the specification fixed when comparing the employment
effects of different types of ARRA spending.
Conley and Dupor (2013) report the smallest employment effects. They construct two
endogenous fiscal policy variables, ARRA spending and lost tax revenue plus increased Medicaid
spending, and two instruments, the formulaic component of highway spending and state tax
revenue cyclicality. In their fungibility constrained specification, the endogenous variable is
collapsed into ARRA spending net of lost tax revenue, such that the employment effect of
a dollar of ARRA aid is constrained to have the same employment effect as an additional
dollar of tax revenue. This specification gives rise to a cost-per-job estimate of $200K. But as
discussed in section 3.1.1, economic theory dictates at most equivalence between state spending
financed by ARRA transfers and a deficit-financed increase in state spending; the fungibility
assumption instead imposes equivalence between ARRA-financed spending and a balanced
budget increase in state spending. Since the presence of either Ricardian or hand-to-mouth
agents will deflate the balanced budget multiplier relative to ARRA-financed spending, theory
suggests the constrained cost-per-job is too high. In their second specification which does not
collapse the endogenous variable, Conley and Dupor (2013) find an employment multiplier 50%
25
The changes in specification include the sample period, whether DC is included, and whether the endogenous
variable is FMAP or total ARRA.
33
larger and closer in magnitude to other papers.
Wilson (2012) develops three formulaic allocation instruments: pre-recession Medicaid
spending as in Chodorow-Reich et al. (2012), the schooling age population which partly deter-
mined the allocation of spending by the Department of Education, and the highway instrument
described in section 4. He reports a headline cost-per-job of $125K. A complication arises in
comparing this number to other studies, however, because it corresponds to additional employ-
ment in February 2010 relative to total announced ARRA state-level spending allocation by
that month, while much of the actual spending occurred later. Using instead actual spending or
spending obligated to specific entities results in lower cost-per-job estimates because spending
as of February 2010 is correlated with spending after February 2010. A simple alternative spec-
ification which elides this problem follows the approach in section 4 and estimates the integral
of additional jobs through some terminal date as a function of spending by that terminal date.
Using March 2011 as the terminal month – the last month in the Wilson (2012) data set and
after more than 80% of the ARRA had been outlaid – but keeping the specification and control
variables otherwise identical to Wilson (2012), I estimate a jobs coefficient of 1.75 (se=0.71).
This estimate translates into a cost-per-job of $57K ($100K/1.75).26
The last cross-state study of the ARRA is Feyrer and Sacerdote (2012). The paper reports
estimates from OLS regressions of employment on ARRA by state and from IV estimates
where ARRA transfers are instrumented using the mean seniority of a state’s congressional
delegation. The paper finds employment effects more than twice as large when using IV.27 To
26
Using instead funding announcements through March 2011, the jobs per $100K spent falls only slightly to 1.42
from 1.75.
27
The instrument in Feyrer and Sacerdote (2012) is the mean seniority of the entire Congressional delegation,
where House members are ordered 1-435 and Senate members 1-100, and not the mean seniority of the state’s
House delegation as reported in the paper. Using either seniority measure separately does not predict spending
allocation. Boone et al. (2014) also investigate the political economy of the distribution of ARRA spending and
34
obtain a result comparable to other studies, I re-estimate the Feyrer and Sacerdote (2012) IV
specification using their data but replacing the dependent variable using equation (3) and find
a jobs coefficient of 1.99 (se=0.74), which translates into a cost-per-job of $50K.
A few studies have examined employment effects of the ARRA at a sub-state level. Unlike
the state-level studies whose data come from reporting by federal agencies of the state allocation
of all ARRA outlays, allocating spending at the sub-state level requires using the recipient
reporting of spending and the location of the recipients. Spending reported by recipients likely
corresponds more closely to the national accounts definition of direct government purchases
than does the full ARRA, which includes transfers to both individuals and state governments.
Dube et al. (2014) use panel regressions at the county level. Unlike the other studies reviewed,
their identification comes solely from controlling for a large set of determinants of county
economic conditions. They find a cost-per-job in the recipient county of $100K but substantial
spillovers across counties, with a cost-per-job including all counties within 120 miles of the
recipient of $30K.28
Finally, Dupor and Mehkari (2016) and Dupor and McCrory (Forthcoming) develop an
instrument for county-level recipiency of ARRA funds based on the formulaic components of the
ARRA. Their instrument forms the basis for the “DM” instrument in table 1. Similar to Dube
et al. (2014), Dupor and McCrory (Forthcoming) report evidence of substantial geographic
spillovers, with the employment effect of $100K in spending rising from 1 job-year in the
recipient’s region to 1.85 when including employment effects in other subregions belonging to
find little evidence of legislative seniority mattering.
28
The ARRA reporting system may partly explain the estimates of large cross-county spillovers. As pointed
out by Garin (2016), vendors reported spending in the county where a project occurred rather than the county
containing the payroll office of the vendor. County-level employment data sets including the Quarterly Census
of Employment and Wages and County Business Patterns instead attribute employment to the county of the
vendor’s payroll office.
35
the same local labor market. Dupor and Mehkari (2016) find a smaller employment effect of
0.95 job-years at the local labor market level.
Summing up, the estimate of 2 job-years per $100K in column (4) of table 1 appears broadly
representative. Put on common footing, the ARRA studies find estimates in the range of 0.76
to 3.93, with a cross-study mean of 2.1 and median of 1.9. With the exception (barely) of Dube
et al. (2014), the confidence intervals of the ARRA studies all overlap.
5.2. Other Evidence
Estimation of geographic cross-sectional multipliers has proceeded in numerous other di-
rections, making use of clever identification strategies and developing new data sets. Table 3
summarizes these studies.
Table 3: Non-ARRA Papers
Geography/
Study/ Jour- Identification Financing/ Result
nal
Persistence
Acconcia et al. Provincial expenditure cuts
Province/ Outside Impact output multiplier of 1.55
(2014), Amer- in Italy following expulsion of
financing/ Transi- [0.84,2.26], cumulative multiplier of
ican Economic Mafia-infiltrated city council
tory 1.95
Review members
$100K spending increases employ-
Adelino et al.
ment by 5.10 (0.58 [0.21,0.94] gov-
(Forthcom- Municipality/
2010 Moody’s recalibration of ernment and 4.52 [1.97,7.07] pri-
ing), Review Outside financing/
U.S. municipal bond ratings scale vate) job-years; income multiplier
of Financial Persistent
of 1.9. Effects are larger when slack
Studies
is higher.
System GMM on annual
Brückner and
Japanese prefecture spend- Prefrecture/ Public investment multiplier of 0.93
Tuladhar
ing data controlling for lagged Mixed financing/ [0.63,1.23], local government expen-
(2014), Eco-
output and prefecture fixed Transitory diture multiplier of 0.78 [0.45,1.11]
nomic Journal
effects
Bucheim and
German stimulus targeted to County/ Outside
Watzinger e100K increases employment by
improving energy efficiency of financing/ Transi-
(2017), Unpub- 4.0 [0.2,7.8] job years
school buildings tory
lished
Clemens and State/ Local
”On-impact” multiplier of 0.29 [-
Miran (2012), State balanced budget rules financing/ Transi-
0.22,0.79]
AEJ:Policy tory
36
1 percent increase in annual ear-
Cohen et al. State/ Out-
Changes in congressional com- marks causes 0.8 [0.6 , 1] percent re-
(2011), Jour- side financing/
mittee chairmanships instrument duction in the representative firm’s
nal of Political Throughout chair-
state-level federal expenditures capital expenditures. Crowding out
Economy man term
smaller when slack is higher.
Corbi et al. Municipality/
Population-based discontinuity in
(2017), Unpub- Outside financing/ Output multiplier of 2
federal transfers in Brazil
lished Transitory
Fishback and
Multiplier of 0.96 [0.31,1.61] when
Kachanovskaya State/ Outside
Shift-share instrument – sensitiv- transfer payments are excluded and
(2015), Journal financing/ Transi-
ity to changes in federal spending 0.83 [0.39,1.27] when transfers are
of Economic tory
included
History
An additional veteran in a state as-
Hausman
State and city/ sociated with 0.3 [0.20,0.41] more
(2016), Amer-
1936 veteran’s bonus Outside financing/ new cars sold; An additional vet-
ican Economic
One-time eran in a city associated with $200
Review
[$73,$327] more residential building
Leduc and
Panel local projection on revision State/ Mixed fi-
Wilson Impact multiplier of 1.4. Cumula-
to present value of federal high- nancing/ Present
(2012), NBER tive multiplier of 6.6
way transfer funds value
Macroannual
State GDP multiplier of 1.43
Nakamura
[0.84,2.02]; region GDP multiplier
and Steinsson State and region/
Regional variation in military of 1.85 [0.90,2.80]; state employ-
(2014), Amer- Outside financing/
buildups ment multiplier per percent of GDP
ican Economic Transitory
of 1.28 [0.80,1.76]. GDP multiplier
Review
is larger when slack is higher.
One year ”Grants multiplier”
Porecelli and Allocation of reconstruction Municipality/
of 0.15 [0.05,0.25] and of 0.36
Trezzi (2016), grants to municipalities following Outside financing/
[0.21,0.52] when earthquake dam-
Unpublished the 2009 ”Aquilano” earthquake One-time
ages are instrumented
Income multiplier of 2.1; $100K
Windfall component of returns State/ Outside
Shoag (2015), spending increases employment by
on state’s defined-benefit pension financing/ Transi-
Unpublished 2.89 [1.25,4.54] job-years. Effects
plans tory
are larger when slack is higher.
Suárez Serrato
County/ Outside Local income multiplier of 1.7-2;
and Wingen- Federal spending due to errors in
financing/ Perma- $100K spending increases employ-
der (2016), local population estimates
nent ment by 3.25 [0.35,6.15] job-years
Unpublished
Shoag (2015) builds a data set of idiosyncratic returns of state pension funds. These returns
relax state budget constraints and empirically predict increased government spending (but not
lower tax revenue). Shoag (2015) therefore uses the pension returns as an instrument for state
spending and finds a $1 increase in spending raises personal income by $2.12 and that $100K
37
of spending raises employment by 2.9 job-years.29 While the first stage indicates states spend
roughly 50% of the windfall in the first year, Shoag argues that private agents are unlikely
to react to the windfall component other than due to the government spending because of an
absence of publicity of state pension returns.
Suárez Serrato and Wingender (2016) start from the observation that a multitude of federal
transfers to local governments depend on local population, but censuses of population by area
occur only every ten years. In the interim, the Census Bureau estimates local population
growth using birth and death records and migration flows. The benchmarking to the Census
count every ten years then induces jumps in federal payments to a local area caused by the
sudden dissipation of measurement error. Suárez Serrato and Wingender (2016) study the
response of local private income and total employment to these jumps in payments and find
an income multiplier of 1.7-2 and a cost-per-job of roughly $31K. Notably, while measurement
error offers an appealing source of exogenous variation in spending changes, the persistence of
these transfers is quite high since future federal funds are also higher as a result of an upward
revision to the population estimate.
Nakamura and Steinsson (2014) adapt the time series approach of measuring the response of
output to increases in federal purchases associated with defense build-ups (Barro, 1981; Ramey
and Shapiro, 1998; Hall, 2009) to a cross-sectional setting. In particular, when defense purchases
rise, they rise by more in states with larger concentrations of defense contractors. Nakamura and
Steinsson (2014) implement a version of equation (1) where the endogenous variable Fs,t consists
of federal defense purchases in state s in year t and the instruments are state-specific loadings
29
Shoag (2015) argues that personal income closely tracks output but provide a more reliable measure of state-
level economic activity over his sample.
38
on the growth of national defense purchases. Their identifying assumption then becomes that
the federal government does not engage in a defense build up because of economic weakness
concentrated in regions more heavily dependent on defense contracting. They estimate a state
output multiplier of roughly 1.4 and a multiplier of 1.9 when expanding the geographic unit
to the region level. The persistence of the purchases is similar to the persistence of a defense
build-up, that is, higher than in a one-time stimulus bill, but lower than a population update.
Two studies use historical variation from spending during the 1930s. Fishback and Kachanovskaya
(2015) examine New Deal spending and transfers using a state-year panel and a shift-share in-
strument for spending in a state. They find income multipliers of close to but below one.
Hausman (2016) uses variation in the geographic distribution of World War I veterans inter-
acted with the large, one-time Veteran’s bonus payment in 1936. While lacking in overall
measure of private spending, he finds substantial increases in auto purchases and new building
in states and cities with more veterans.
Adelino et al. (Forthcoming) exploit a change in borrowing costs resulting from a recalibra-
tion of municipal bond ratings by Moody’s. They find a local income multiplier of 1.9 at the
county level and a cost-per-job of $20K. While the recalibration implies a persistent lowering
of borrowing costs, the magnitude of the decline in interest payments appears too small for a
response of private consumption to the relaxation of the county’s budget constraint to explain
the large employment effects.
Leduc and Wilson (2012) study the response of state output to innovations in the present
value of federal highway grants. They find large output multipliers, but with the caveat they
cannot precisely estimate the response of state spending to the federal grants. Using their
39
most conservative results, they find an impact response of $1.40 of state GDP to an increase
in present value of spending of $1 and a cumulative multiplier of 6.6. The persistence of the
output response suggests part of the cumulative multiplier reflects higher productivity from
the capital improvements in addition to any short-run demand effects.
A few studies have used data from outside the U.S. Acconcia et al. (2014) exploit the intro-
duction of an anti-corruption law in Italy which resulted in the dismissal of city councils and
their replacement by external commissioners who reduced public expenditure. They estimate
an output multiplier of 1.6 to 2.0, where the higher number includes lagged government spend-
ing effects. Because the central government finances most local expenditure, these estimates
correspond to outside-financed multipliers despite the determination of spending at the local
level. Brückner and Tuladhar (2014) use a system GMM estimator to study variation in an-
nual spending across prefectures in Japan in the 1990s. Effectively, identification comes from a
timing assumption similar to that in Blanchard and Perotti (2002) that fiscal policy not have
a forward-looking component. They find multipliers below but close to 1. Interestingly, they
find larger multipliers for locally-financed than centrally-financed public investment. Porecelli
and Trezzi (2016) exploit discontinuities in the provision of reconstruction grants to municipal-
ities following the 2009 L’Aquila earthquake in Italy. While their “grants multiplier” of 0.3 is
lower than most other studies, if one assumes municipalities would have engaged in the same
rebuilding effort with or without the grants, then this 0.3 estimate corresponds more directly
to a pure windfall transfer multiplier and as such is only slightly larger than the calibrated
estimates discussed in section 3.1.1. Corbi et al. (2017) exploit several discontinuities in the
formula mapping local population to transfers from the federal government in Brazil. They es-
40
timate a cost per job year of roughly $8,000, with three-quarters of the additional employment
in the private sector. Using the production function approach, this magnitude translates into
an output multiplier of roughly 2.
Finally, two important studies find much smaller or even negative effects of local spending.
Clemens and Miran (2012) use variation in the strictness of state balanced budget requirements
and find a spending multiplier with a point estimate close to zero and an upper bound of 0.8.
They interpret the smaller estimated multiplier as reflecting the absence of a windfall transfer
since, while a laxer balanced budget requirement allows a state to run a temporarily larger
deficit, it does not affect the local region’s intertemporal budget constraint. Even so, the trans-
fer component of the other studies reviewed appears by itself too small to explain the difference,
suggesting other econometric or institutional factors may also matter. Cohen et al. (2011) ex-
ploit the increase in federal spending in a state when a member of the state’s Congressional
delegation becomes the chair of an important committee. They estimate statistically signifi-
cant negative effects of spending on investment, employment, and sales at publicly-traded firms
headquartered in the state. Cohen et al. (2011) interpret their results as reflecting a wealth ef-
fect from the windfall transfer. However, they also report negative albeit imprecisely estimated
effects on overall state output which would require more than just a labor supply response to
justify.
6. What We’ve Learned
Informativeness for national multiplier. Cross-sectional multipliers can be large. A cross-
study average necessarily ignores aspects such as persistence of spending and regional openness
41
which differ across studies and likely affect the estimated multiplier. Nonetheless, using the
relationship in equation (8) to translate employment multipliers into output multipliers and
aggregating over all studies described in tables 2 and 3 for which I could calculate an output
multiplier, the mean output multiplier is 2.1 and the median is 1.9.30 This magnitude closely
matches the updated estimates based on the ARRA in section 4. Removing the two studies
(Suárez Serrato and Wingender, 2016; Adelino et al., Forthcoming) which measure responses
to persistent increases in spending, the mean (median) multiplier is 1.8 (1.9). Restricting
to studies already published in peer-reviewed journals as a crude quality filter gives a mean
(median) multiplier of 1.6 (1.6).
According to the theory reviewed in section 3, a deficit-financed cross-sectional multiplier
provides a lower bound for the closed economy zero lower bound deficit-financed multiplier.
Accounting for the outside financing of spending in many of the studies might reduce the
lower bound by about 0.1. Thus, using the mean estimate of 1.8 for the studies based on
transitory spending, the cross-sectional evidence suggests a closed economy zero lower bound
deficit-financed multiplier of about 1.7 or above.
Is a national multiplier of 1.7 large? In a recent review article, Ramey (2011a) concludes
the multiplier for a deficit-financed increase in government purchases similar to the ARRA,
that is, the multiplier for a temporary, deficit-financed increase in spending when monetary
policy is constrained, “is probably between 0.8 and 1.5. Reasonable people can argue, however,
that the data do not reject 0.5 or 2.0.” If this range serves as a prior, then the evidence from
30
Providing a confidence band for the cross-study mean or median is complicated by the possibility of correlation
across studies, especially for papers studying the ARRA, and I do not attempt it. The studies reviewed in table 2
and table 3 and excluded from the cross-study mean and median are Cohen et al. (2011), Hausman (2016), Leduc
and Wilson (2012), Porecelli and Trezzi (2016), and Bucheim and Watzinger (2017).
42
cross-sectional multiplier studies ought to move posteriors toward the upper end of the range.
Two factors may explain the larger multiplier implied by cross-sectional studies than that
based on time series evidence. First, most cross-sectional studies explicitly identify quasi-
experimental variation in spending. These studies may therefore use cleaner variation than is
available in the time series. Second, a “lean against the wind” monetary policy dampens the
national multiplier and it may be difficult to extract the passive monetary policy multiplier from
time series studies which span diverse monetary policy regimes. In this sense, cross-sectional
variation may offer a better laboratory for studying what happens when monetary policy does
not react.31
State-dependence. Many of the studies also shed light on an important debate on whether
and why multipliers may be state dependent. Here again, the time series literature has not
reached a consensus (Auerbach and Gorodnichenko, 2013; Ramey and Zubairy, Forthcoming).
Cohen et al. (2011); Shoag (2015); Nakamura and Steinsson (2014); Dube et al. (2014); Adelino
et al. (Forthcoming) all test for and find evidence of higher multipliers or less crowd-out in
regions and periods with more unused resources. Because the cross-sectional studies hold the
response of monetary policy fixed, passive monetary policy in slack periods, as emphasized in
Christiano et al. (2011) and Woodford (2011), cannot explain the findings of state-dependent
multipliers in these studies. Instead, other forces related to slack such as lower factor prices or
less congested labor markets appear also to matter (Michaillat, 2014).
31
One recent study of national multipliers in Japan which explicitly distinguishes zero lower bound episodes in-
deed finds higher multipliers in such periods, with a magnitude in line with the cross-sectional evidence (Miyamoto
et al., 2017).
43
Other policies. Cross-sectional multipliers inform the effects of a broader set of policies than
just national counter-cyclical stimulus. For example, high and uneven unemployment in the
euro area has renewed interest in further fiscal integration. How effective as counter-cyclical
stimulus would be spending by the European Union in targeted regions with high cyclical
unemployment? Cross-sectional multiplier studies provide a direct and generally optimistic
answer to this question.
The evaluation of place-based policies offers another example. Similar to many of the cross-
sectional studies, place-based policies direct federal resources toward particular geographic
areas.32 On the other hand, place-based policies typically combine grants for spending with
targeted hiring incentives and other business tax breaks, involve very persistent interventions,
and apply to very small geographic areas. Relative to cross-sectional multiplier studies, the
small geographic concentration reduces the effects of transfers into the region on local output
but the longer persistence means the transfers are larger. The persistence has also led the
place-based literature to analyze spatial equilibrium models which allow for a migration re-
sponse, an aspect ignored in the theoretical treatments of cross-sectional multipliers, but at the
expense of abstracting from short-run demand effects. These differences aside, the evidence
from cross-sectional multiplier studies appears more optimistic of the scope for positive local
effects than are many studies of placed-based policies. Both literatures would benefit from
greater integration.
32
Empowerment Zones are the most well known. See Glaeser and Gottlieb (2008) and Neumark and Simpson
(2015) for recent surveys of place-based policies.
44
7. Lessons for Future Research
While much progress has occurred, there remains scope for further integration of empiri-
cal and theoretical investigations of cross-sectional multipliers. One aspect concerns empirical
studies of natural experiments in which spending rises without a concomitant increase in the lo-
cal tax burden. These studies should quantify the magnitude of the outside transfer or windfall.
A useful summary metric is the ratio of the annuity value of the transfer to the contempora-
neous increase in government spending. These studies should also discuss the salience of the
windfall component. Did private agents plausibly understand that they had received a transfer
of resources or a windfall? On the theory side, the rough lower bound result depends on the
small difference between outside-financed and locally-financed multipliers in modern macroe-
conomic models. Future research should explore and try to quantify other mechanisms which
might amplify this difference.
More research is also needed to quantify the differences between deficit-financed local mul-
tipliers and national zero lower bound multipliers. Most important, we have little evidence of
how relative prices change in response to local government spending shocks. While regional
price data in the United States is haphazard, studies of euro area members each of which
collects its own CPI may prove more fruitful.
Finally, while the dependence of “the” government purchases multiplier on other variables
such as the monetary policy response is widely recognized, empirical studies have paid less
attention to heterogeneity stemming from what the government actually purchases.33 This
aspect may matter even more in cross-sectional studies where the source of variation is the
33
Boehm (2015) is a recent exception.
45
quasi-randomness of the allocation of a particular government program; even if the estimation
uses instrumental variables with total spending the endogenous variable, the LATE theorem
(Imbens and Angrist, 1994) means that the estimated multiplier depends on the source of
variation. On the other hand, budgetary fungibility would negate such differences. Where
relevant, future studies should highlight the source of transfers or increase in purchases both
to better compare themselves to the literature and to facilitate future research into the effects
of different types of policies.
46
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