Valerie A. Ramey | Macro Paper Warehouse

Can Government Purchases Stimulate the Economy?

This essay surveys the state of knowledge on the government-spending multiplier as of 2011, drawing together theory, U.S. aggregate time-series evidence, and the newer cross-state/cross-locality “natural experiment” literature, to answer the question most relevant to the post-2008 stimulus debate: how much output does a temporary, deficit-financed increase in government purchases buy? Ramey first shows that “the multiplier” is not one number: in neoclassical models the multiplier operates through a negative wealth effect on labor supply and can range from as low as -2.5, when spending is temporary and financed by concurrent distortionary taxes, to about 1.2 for a permanent increase financed by lump-sum taxes, because the size and even sign of the multiplier depends critically on the persistence of the spending and how it is financed; in New Keynesian models the multiplier is typically smaller than in traditional Keynesian models (often at or below one) unless the model assumes widespread rule-of-thumb consumers and demand-determined employment, or unless the nominal interest rate is stuck at the zero lower bound, in which case rising expected inflation lowers the real interest rate and multipliers well above one become possible (Christiano, Eichenbaum, and Rebelo’s estimate peaks at 2.3). Turning to the data, she reviews a range of aggregate U.S. time-series studies – from the large-scale econometric models of the 1960s through modern structural VARs using military-spending instruments, narrative “news” shocks, and Blanchard-Perotti-style identification – and finds that, despite substantial differences in sample, experiment, and identification strategy, most estimates cluster between roughly 0.6 and 1.8, with standard errors that are always large; she argues the lower end of this range mostly reflects episodes (such as the Korean War) in which spending was partly tax-financed, and that after truncating for that and for concerns about persistence and measurement in the highest estimates, the range most relevant to a temporary, deficit-financed increase is 0.8 to 1.5, with multipliers likely toward the top of that range during severe recessions. She also surveys the newer literature using cross-state and cross-region panel data (military contracts, ARRA allocations, New Deal spending), which mostly finds income multipliers of about 0.5 to 2.0 and implied costs of roughly $25,000-$35,000 per job created, while cautioning that these local multipliers answer a conceptually different question from the aggregate multiplier and require an explicit model (of the kind developed by Nakamura and Steinsson 2011 and Shoag 2010) to translate into an aggregate estimate. The essay closes by noting that despite the proliferation of estimates, there remains no consensus on the underlying transmission mechanism – some studies find consumption falls in response to spending increases, consistent with the neoclassical wealth effect, while others find it rises, consistent with rule-of-thumb consumers – and that none of the multiplier estimates reviewed speaks to the welfare consequences of stimulus spending, which would require additional assumptions about mechanisms and about whether government purchases enter the utility function.

Macroeconomic shocks and their propagation

This 2016 Handbook of Macroeconomics chapter by Valerie Ramey is a survey and methodological stock-taking exercise on how macroeconomists identify structural shocks to monetary policy, fiscal policy (government spending and taxes), and technology, and how those shocks propagate through the economy — organized around the question Cochrane (1994) posed of whether researchers are “destined to remain forever ignorant of the fundamental causes of economic fluctuations,” to which Ramey’s answer is “no.” Rather than introducing a new identification scheme, the chapter sets out a common reduced-form/structural framework (reduced-form residuals e_t = Bepsilon_t, impulse responses C(L) = A(L)^-1B) and classifies the literature into roughly nine identification strategies — recursive/Cholesky orderings (with the policy variable ordered either last, as in Christiano-Eichenbaum-Evans, or first), non-recursive structural restrictions, narrative methods, high-frequency identification, external-instrument/proxy SVARs, long-run restrictions, sign restrictions, and factor-augmented VARs — and then re-estimates or directly compares many of them on overlapping or updated data. For monetary policy, a comparison of eleven leading published methods on their original samples finds trough effects of a 100-basis-point funds-rate increase on output/industrial production ranging from a positive, statistically insignificant response (Uhlig’s 2005 sign-restriction estimate) to declines of several percent (Romer-Romer’s 2004 narrative measure implies -4.3% at 24 months; Barakchian-Crowe’s 2013 high-frequency estimate implies -5% at 23 months), with no consensus on the “true” magnitude. Ramey’s own re-estimation of the Christiano-Eichenbaum-Evans-style recursive VAR shows the effect shrinking from a -0.48% trough (accounting for 6.6% of the output forecast-error variance at 24 months) over 1965-1996 to a -0.20% trough (0.5% of variance) over 1959-2007, and turning expansionary when the sample is restricted to 1983-2007. She then subjects the Gertler-Karadi (2015) high-frequency proxy instrument to validity checks and finds it has a nonzero mean (-0.013), is serially correlated (AR(1) coefficient of 0.31, robust SE 0.11), and is predictable from Federal Reserve Greenbook forecasts (R-squared of 0.21, p=0.027) — evidence that the instrument is contaminated by the Fed’s private information rather than being a clean exogenous surprise — leading her to conclude that what is now identified as a monetary policy shock is “really mostly the effects of superior information on the part of the Fed, foresight by agents, and noise.” For fiscal shocks, government-spending multiplier estimates cluster mostly between 0.6 and 1.5 once computed correctly as the integral of the output response over the integral of the spending response (rather than a peak-to-impact ratio), while tax-multiplier estimates vary more across method, from roughly -0.5 to -0.8 (SVAR-based estimates using outside output elasticities) up to about -3 (Romer-Romer 2010 narrative and Mertens-Ravn 2014 proxy-SVAR estimates). For technology shocks, the chapter documents low correlations between shocks extracted from different identification approaches and finds that investment-specific technology (IST) and marginal-efficiency-of-investment (MEI) shocks — including news about future IST change (Ben Zeev-Khan 2015, estimated to explain 73% of output variance at 8 quarters in one specification) — tend to matter more for business-cycle fluctuations than neutral total-factor-productivity shocks, whose estimated importance ranges from negligible (Galí 1999) to more than 40% of output variance depending on method. A combined VAR that Ramey estimates herself, incorporating leading fiscal, technology, and monetary shock measures together over 1954-2005, finds that the Ben Zeev-Khan IST-news shock is the single most important driver of both output and hours (accounting for up to 40% of the hours forecast-error variance at 8 quarters), that the Justiniano-Primiceri-Tambalotti MEI shock explains 42% of output variance on impact falling to 24% within a year, that the federal funds rate accounts for up to 8% of output and 18% of hours variance, and that all the included shocks together explain 63-79% of the variance of output and hours at horizons of 4-20 quarters — evidence Ramey reads as showing genuine, if incomplete, progress against the identification problem Cochrane posed two decades earlier, even as she stresses that none of the individual identification strategies commands full consensus.

The Cost Channel of Monetary Transmission

This 2001 NBER Macroeconomics Annual paper by Marvin Barth and Valerie Ramey tests whether monetary policy operates through a supply-side “cost channel” – in which a monetary contraction raises firms’ working-capital financing costs and thereby raises production costs and prices – in addition to the conventional demand channel, using two separate empirical frameworks. The first is an aggregate six-variable quarterly VAR (1959:Q1-2000:Q3) that uses long-run restrictions following Gali (1999) to identify a technology shock (the only shock permitted a permanent effect on labor productivity) and a monetary policy shock (the federal-funds-rate innovation orthogonal to it); the authors show that the estimated responses to a contractionary monetary shock – falling labor productivity, falling hours, procyclically falling real wages, and a temporary price-level increase – resemble the responses to a negative technology shock far more than the responses to an identified demand shock (a defense-spending increase), which instead raises output and lowers real wages countercyclically. The second framework is a seven-equation industry-level pseudo-panel VAR (monthly, 1959-2000, 7 lags, with a macro block of industrial production, the PCE deflator, commodity prices, M2, and the federal funds rate, and an industry block of output and the price-to-wage ratio for 21 two- and three-digit manufacturing industries) that tests whether a contractionary funds-rate shock raises the industry price-to-wage ratio (P/W) – the signature of a supply-side cost shock – even as output falls. Over the full sample, 10 of 21 industries show P/W rising for more than half of the first 24 months, 6 significantly at the 10% level; the effect is far stronger before 1979 (15 of 21 industries significant) than during 1983-2000 (only 3 of 21 significant), a period split the authors attribute to financial deregulation, the end of Federal Reserve “credit actions” that had directly restricted bank lending, and the shift to floating exchange rates. Consistent with this timing, in a standardized 25-basis-point funds-rate shock the pre-Volcker output trough is almost four times as deep and the “price puzzle” (prices rising after a contractionary shock) persists for over two years, versus a roughly nine-month funds-rate reversion and largely flat prices after 1983. The authors motivate the mechanism with a working-capital calculation (Federal Reserve Flow of Funds and BEA data, averaged 1959-2000): gross working capital equals about 17 months of final sales and net working capital about 11 months, and a simple labor-demand equation implies that, holding real wages fixed, a 100-basis-point rate rise lowers labor demand by about 3% when the capital cost share is 0.3 – or by about 15% once a credit-channel-style widening of external financing spreads is layered onto the roughly 400-basis-point average funds-rate increase seen over a Romer tightening episode. Cross-industry heterogeneity in the price-to-wage response correlates positively with industries’ interest-expense burden relative to sales (correlation of about 0.53 in an early-1970s cross-section, about 0.43 in a 1990 cross-section), which the authors read as further evidence linking the price response to financing costs specifically. They test and argue against sticky-price/flexible-wage and misspecified-Fed-reaction-function explanations for the same facts, but explicitly acknowledge that countercyclical-markup theories are observationally equivalent to their cost-channel story without direct marginal-cost data, and they frame the cost channel as a short-run phenomenon layered on top of the standard demand channel rather than a challenge to long-run monetary neutrality.