Government Spending Multipliers in Good Times and in Bad: Evidence from US Historical Data

The authors argue that “long samples of historical data for the United States meet this challenge well since US historical data include many more periods of slack, one more extended period near the zero lower bound, and much larger variations in government spending during world wars” (Sec. II.A) than the post-WWII sample, where informative identification of state-dependent multipliers requires that “the states span a sufficient portion of the sample and that the exogenous changes in government spending be spread across the states.” They address the natural objection that wartime data are “abnormal” by invoking Friedman’s (1952) argument that large, discrete historical episodes are “peculiarly valuable” precisely because ordinary peacetime data vary too smoothly to separate systematic effects from noise, while acknowledging confounding factors specific to each war (conscription, rationing) that they address in case studies and sample-exclusion checks.

The baseline instrument is an extended version of Ramey’s (2011) “military news” series, which “captures only news about changes in military spending” and leads government spending to rise only with a delay; the alternative is the Blanchard and Perotti (2002) shock, identified from a Cholesky decomposition that assumes government spending does not react within the quarter to other macro variables, and which “lead[s] to immediate rises in government spending with peaks close to impact.” The trade-off is explicit: the Blanchard-Perotti shock is “more sensitive to potential measurement errors in the historical data and subject to the critique that it is likely to have been anticipated,” and because it is constructed directly from the (historically noisy) government spending series, any measurement error in that series is inherited by the shock, biasing multiplier estimates toward zero (attenuation bias) — which the authors note is consistent with the Blanchard-Perotti-based multipliers being systematically lower than the military-news-based ones throughout the paper.

First, converting an estimated elasticity (from log variables) into a dollar multiplier using the sample-average ratio of GDP to government spending (Y/G) is sensitive to that average: in the post-WWII sample Y/G averages 5, but in the 1889–2015 sample it averages close to 8, so “we could estimate the same elasticity of output with respect to government spending but derive much higher multipliers simply because the mean of Y/G was so much higher.” They avoid this by following Gordon and Krenn’s (2010) transformation of dividing variables by trend GDP rather than taking logs. Second, they argue multipliers should be computed as the ratio of the integral (cumulative) output response to the integral spending response, not — as in the original Blanchard and Perotti (2002) definition still widely used — as the ratio of peak output response to the initial spending shock, since “the Blanchard-Perotti method of reporting multipliers tends to produce higher estimates of multipliers relative to the cumulative method.” They show the cumulative multiplier can be estimated directly and efficiently in a one-step instrumental-variables regression, which also permits combining multiple instruments.

Slack is defined by whether the unemployment rate exceeds a threshold (6.5 percent at baseline, following Owyang, Ramey, and Zubairy 2013), which the authors distinguish explicitly from NBER recession dating, noting that “only half of the quarters that are official recessions are also periods of high unemployment.” Using the military news shock, the estimated 2- and 4-year cumulative multipliers are “very similar across the two states, both around 0.6 or 0.7,” with no statistically significant difference (reported via both HAC-robust and weak-instrument-robust Anderson-Rubin tests). Using the Blanchard-Perotti shock, multipliers are lower overall (0.4–0.5 in the linear case) and there is a statistically significant difference across states, but “the estimates imply that multipliers differ across the states not because they are so elevated in high-unemployment states but because they are so low in low-unemployment states. In all cases, they are below unity.”

Across a battery of alternative specifications — a time-varying (HP-filtered) unemployment threshold, an 8 percent unemployment cutoff, NBER recession dates, a smooth-transition weighting of output growth, added tax controls, exclusion of the WWII rationing period, and restriction to the 1947–2015 post-WWII subsample — the authors “still get multipliers less than one across both recession and expansion regimes and do not find any evidence of higher multipliers in recessions versus expansions.” The main exception is informative about data limits rather than about the multiplier itself: when WWII is excluded, estimated high-unemployment-state multipliers rise toward or above one (up to 1.62 for the Blanchard-Perotti 4-year multiplier) but with such large standard errors that “there is no statistically significant difference (even at the 10 percent level) between multipliers across the two states,” and restricting to the post-WWII subsample alone yields weak instruments and even negative point estimates that the authors flag as “not reliable.”

They classify 1932q2–1951q1 and 2008q4–2015q4 as “ZLB or extended monetary accommodation times,” identified by comparing actual interest rates to a Taylor-rule benchmark rather than using a literal zero cutoff, and explicitly exclude the early 1930s and the WWI-era gold-standard period from this definition. In the full historical sample, using the military news shock, “we see little difference in multipliers in the ZLB state” (0.64–0.71 near the ZLB versus 0.66–0.71 in normal times). Using the Blanchard-Perotti and combined-instrument specifications, multipliers are estimated to be higher in the ZLB state (0.63–0.77) than in normal times (0.10–0.26), with the difference statistically significant by the HAC test — but, as with the slack results, the gap is “due not to elevated multipliers in the ZLB but to multipliers estimated to be near zero in the normal states.”

This is the one specification in the paper where multipliers clearly exceed unity: using the military news shock alone, the 2-year ZLB multiplier is estimated at 1.40 (HAC standard error 0.153) versus 0.63 in normal times, a difference the authors describe as statistically significant by the HAC test, “though they are still below unity” for the Blanchard-Perotti-based estimate in the same exercise (1.08, with a very large standard error of 0.749). Using both instruments combined, the 2-year multiplier reaches 1.60. The authors are careful to note the instrument-relevance caveats behind this result: once WWII is excluded, the sample loses the long ZLB-period military news shocks that WWII itself supplied, so remaining inference rests more heavily on fewer, noisier observations.

The authors attribute the gap to “the simplifying assumptions about state transitions that they use to convert their smooth transition VAR (STVAR) estimates into impulse responses,” specifically the baseline assumption that the economy remains in whichever state (recession or expansion) it starts in for the entire 20-quarter horizon over which the multiplier is computed. They argue this is a reasonable approximation for expansions (which last years) but not for recessions, which “have a mean duration of only 3.3 quarters” by Auerbach and Gorodnichenko’s own definition — so the assumption effectively forecasts ever-rising output after a recession-state shock (since recessions are forecast to end and output to recover) and attributes that mechanical mean-reversion to the fiscal shock itself. Applying the Jordà method directly to Auerbach and Gorodnichenko’s own data, sample, and identification, the authors obtain a 5-year cumulative multiplier of 0.84 — not an elevated recession multiplier — and show that allowing the state to transition endogenously (rather than assuming it is frozen) using the STVAR’s own parameter estimates brings the recession multiplier “around unity.”

Yes: applying a TVAR to the historical sample, under the assumption that the economy does not switch states over the relevant horizon — which the authors note is far more data-consistent for their ZLB episodes, since “average duration of a ZLB period is about 52 quarters” — the TVAR and Jordà methods “give surprisingly similar results… with multipliers between 0.6 and 0.8 in the ZLB state for the full historical sample.” For recession states defined by NBER dates (rather than their baseline slack threshold, for which the TVAR’s roots were explosive), the two methods are again close, with the TVAR showing no evidence of an elevated recession multiplier either.

They state explicitly: “World War II government spending did help lift the economy out of the Great Depression, not because multipliers were so large, but because the amount of government spending was so great. Although multipliers may be modest in magnitude, they are positive.” This reframes the standard narrative as a statement about the sheer scale of wartime spending rather than about an unusually high recession-era multiplier.

The authors flag three limits explicitly: (1) “we are forced to use data determined by the vagaries of history, so we do not have a controlled experiment”; (2) because the military news shock measures only changes in defense spending and the Blanchard-Perotti shock mixes together all types of government-purchase shocks, “our results do not inform us about the size of multipliers on specific classes of government outlays, such as transfer payments or infrastructure spending”; and (3) “because the episodes we studied were characterized by certain paths of taxes, the results are not immediately applicable to the case of deficit-financed stimulus packages or fiscal consolidations.”