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Note: Multipliers are based on evidence reviewed in Bivens (2011) and Bivens (2012). Specifically, the multiplier for infrastructure investments is 1.6, the muliplier for progressive tax increases is (-) 0.9, the multiplier for regressive tax increases is (-)0.35, the multiplier for transfers is 1.6, and following Bivens (2012), 20 percent of the stimulative effect of investments driven by regulatory mandates are crowded out. For employment impacts, we assume each percentage point addition to GDP adds 1.2 million jobs to the economy. The total spending figures are based on the infrastructure investment scenarios described in the text.
To estimate the employment impacts stemming from increased economic activity, we start with the evidence reviewed in Bivens (2011) estimating each 1 percent of generic GDP increase in economic activity will generate 1.2 million additional jobs. So, the $29 billion in additional annual spending spurred by infrastructure investment leads to 216,000 net new jobs created (primarily by the end of the first year, with the new increased level essentially sustained over the course of the investment period).
Columns (2) through (4) then examine the net impact of financing this increase in spending with progressive revenue increases, regressive revenue increases, and cuts to government transfer payments, each in an amount equal to the $30 billion boost to infrastructure spending. For each, we use multipliers based on the evidence examined in Bivens (2011). For regressive tax increases (by which we mean revenue raised disproportionately from lower and moderate-income taxpayers), we average the multipliers estimated for across-the-board payroll tax cuts and a refundable tax credit, yielding a multiplier of 0.9. For progressive tax increases (revenue raised disproportionately from higher-income taxpayers), we average the multipliers that were estimated based on the overall extension of the 2001 and 2003 tax cuts and a corporate tax cut (specifically, allowing accelerated depreciation of plant and equipment for tax purposes), yielding a multiplier of 0.3. Finally, for government transfers, we average the multipliers for food stamps (officially the Supplemental Nutrition Assistance Program, or SNAP), unemployment insurance, and one-time lump-sum payments to retirees, yielding a multiplier of 1.6.
Note: Multipliers are based on evidence reviewed in Bivens (2011) and Bivens (2012c). Specifically, the multiplier for infrastructure investment is 1.6, the muliplier for regressive tax increases is (-)0.9, the multiplier for progressive tax increases is (-)0.35, the multiplier for transfers is 1.6, and following Bivens (2012c), 20 percent of the stimulative effect of investments driven by regulatory mandates are crowded out. For employment impacts, we assume each percentage-point addition to GDP adds 1.2 million jobs to the economy. The total spending figures are based on the infrastructure investment scenarios and are annual gains taking place over the next decade as described in the text.
Note: Multipliers are based on evidence reviewed in Bivens (2011) and Bivens (2012c). Specifically, the multiplier for infrastructure investments is 1.6, the muliplier for regressive tax increases is (-)0.9, the multiplier for progressive tax increases is (-)0.35, the multiplier for transfers is 1.6, and following Bivens (2012c), 20 percent of the stimulative effect of investments driven by regulatory mandates are crowded out. For employment impacts, we assume each percentage-point addition to GDP adds 1.2 million jobs to the economy. The total spending figures are based on the infrastructure investment scenarios and are annual gains taking place between 2014 and 2020 as described in the text.
A series of attempts to do this came from John B. Taylor (2011), who used aggregate time series evidence on personal income and consumption to estimate the impact of the tax rebates and some social transfers (particularly the increase in unemployment benefits) contained in ARRA, along with tax rebates that were passed in 2001 and 2008 in the name of providing fiscal support to the economy. Taylor used these results to argue that one could not reject the hypothesis that the tax rebates and transfers had no impact on personal consumption spending.
The Feyrer and Sacerdote (2011) results are not precisely estimated (the overall multiplier for the stimulus package in various specifications runs from 0.5 to 2), but across a wide range of specifications the results are positive and statistically significantly different from zero.
Further, the specific regression estimated by Conley and Dupor (2011) makes their results not directly comparable to the other state-based econometric estimates of the specific impact of ARRA. Instead, their preferred econometric specification uses the difference between state aid received by ARRA and negative state revenue shocks as the key independent variable. This specification seems more appropriate for answering a general question as to how state employment is affected by (net) negative revenue shocks, but, given the state-specific shock, it does not then tell us how ARRA aid specifically impacted employment growth. The simplest way to state the inability to directly compare the Conley and Dupor (2011) studies and those of others in this vein is that the estimated multipliers cannot be compared because the multiplicands are different.
Given the failure to find statistically significant results from their measures of ARRA spending net of state and local contraction, neither Cogan and Taylor (2012) nor Conley and Dupor (2011) can actually reject the argument that the simple size of ARRA was insufficient to measurably impact state-level trends in economic activity and employment, and not that the marginal effectiveness of a dollar spent by ARRA was low. This is an important point. Cogan and Taylor (2012) and Conley and Dupor (2011) are essentially assuming that states would not have cut back their own spending as much had ARRA funds not been allocated to them; this is the heart of their argument about fungibility. But, as shown by McNichol (2012), even with the ARRA state aid, state and local governments had very large budget shortfalls in 2009 and 2010 (and indeed are expected to see shortfalls for years to come). Given that most states have balanced budget requirements, this means that one cannot plausibly say that state spending would have been higher in the absence of the ARRA funds. In fact, relative to any plausible counterfactual, state spending must have been higher following the receipt of Recovery Act funds.
To argue that the Cogan and Taylor (2012) and Conley and Dupor (2011) papers are not estimating comparable multipliers to other state-based studies is not to say that their findings are of no note to applied macroeconomists and policymakers. The CBO (2012), for example, has actually reduced its estimate of the likely impact of infrastructure spending increases that are managed through grants to state and local governments precisely because of the worry that these governments will reduce their own spending in response to the grants. However, this does not mean that assessments of the all-else-equal impact of infrastructure spending have been reduced because of economic evidence. Rather, it means that policymakers should strive to ensure (perhaps through maintenance of effort requirements for the receipt of federal grants-in-aid) that state and local governments do not sterilize any of the stimulative effect of grants by reducing their own spending. 2b1af7f3a8