A Reconsideration of Investment Behavior Using Tax Reforms as Natural Experiments

The paper opens by noting that both the user-cost-of-capital and q approaches to investment – despite offering “a structural link between tax policy parameters…and investment through the user cost of capital” – “have not proved empirically successful,” with q models in particular yielding “very small estimated effects of q on investment, implying implausibly high estimates of the cost of adjusting the capital stock.” The authors argue the core problem is a measurement-error issue common to both approaches: because tax reforms are infrequent and hard to predict with standard linear-projection techniques, and because fluctuations in a firm’s market value (used to proxy marginal q) need not track fluctuations in expected future profitability, conventional estimation strategies confound genuine structural responses with noise in q or the user cost of capital.

The authors’ solution exploits the fact that “firms knew with certainty what the key tax variables for 1987 would be in September 1986; they could read them in the newspaper” – so that immediately following a major, discrete tax reform, the econometrician can accurately measure firms’ relevant tax-driven expectations without needing to forecast future tax policy at all. They use firm-level panel data rather than aggregate time series for two reasons: cross-sectional variation in investment opportunities and the cost of investing is much richer at the firm level, and – critically – while the aggregate level of tax policy is not plausibly exogenous to investment (policymakers “introduced an investment tax credit when investment was perceived to be ’low’ and removed [it] when investment was perceived to be ‘high’”), the relative tax treatment of different asset types within a reform, driven mainly by differences in depreciation schedules, is far less likely to be endogenous to any individual firm’s investment decisions.

A tax change is classified as “major” if the economy-wide tax wedge (1-F, where F is the present value of tax savings from depreciation allowances and the investment tax credit) moved by at least 10 percent, no similarly large shift occurred in the adjacent years, and the change was largely unanticipated – criteria that identify the Kennedy tax cut (1962), the 1971 reform, the Economic Recovery Tax Act (1981), and the Tax Reform Act (1986). As preliminary, informal evidence that this cross-sectional tax variation matters, the authors plot forecast errors for disaggregated equipment-investment series against forecast errors for a simplified user-cost variable in each major reform year, and find “a negative correlation between the forecast errors, consistent with the neoclassical theory” – asset categories experiencing an unexpectedly larger fall in user cost show an unexpectedly larger rise in investment, and vice versa.

Conventional fixed-effects OLS and GMM estimates of the tax-adjusted q model yield a coefficient on Q of only about 0.025 to 0.057 – small but statistically significant – which the authors note is consistent with previous studies but, under the Hayashi-Summers interpretation of q, implies adjustment costs so large that “Summers’ preferred estimate…implied that a one-dollar increase in investment leads to between one and five dollars of adjustment costs,” an implausible magnitude given that adjustment costs should be a cost of installing capital, not a multiple of its purchase price.

Constructing a modified variable, QT, that holds the non-tax components of q fixed at their values two years earlier (so that remaining variation comes essentially only from tax parameters), and estimating a separate regression for each year, the authors find the coefficient on tax-adjusted q is positive and statistically significant specifically in the years immediately following each of the four major reforms – ranging from 0.874 (1963, after the Kennedy cut) down to 0.470-0.613 in the other three major-reform years – while “in the nonreform years, we find no significant effect of tax-adjusted q on firm behavior.” Interpreted through the same Hayashi-Summers framework, these larger coefficients imply that “an extra dollar of investment will add between 0.05 and 0.12 dollar of adjustment costs,” an order of magnitude smaller, and far more economically sensible, than the implied costs from conventional q-model estimates.

The user-cost-of-capital specification, estimated using the same reform-year identification strategy, yields “large and statistically significant” coefficients on the user cost of capital in the years following major reforms, paralleling the tax-adjusted q results; averaging across these estimates and using the sample’s mean investment-capital ratio and user cost (both near 0.25), the authors calculate an implied elasticity of aggregate equipment investment with respect to the user cost of capital of about -0.66.

Adding a twice-lagged cash-flow-to-capital ratio to the tax-adjusted q specification leaves the Q coefficients largely unchanged, while the cash-flow coefficient itself is “positive and statistically significant,” consistent with Fazzari, Hubbard, and Petersen’s earlier finding that investment is sensitive to internal funds even after controlling for q. Interacting cash flow with a dummy for firms that paid no dividends in the prior period (a common proxy for being financially constrained, following Fazzari, Hubbard, and Petersen) shows this extra cash-flow sensitivity is not uniform: it “follows a clearly discernible pattern – investment by non-dividend-paying firms is much more sensitive to cash flow during recessions,” which the authors read as consistent with models (Gertler and Hubbard; Oliner and Rudebusch) in which net worth binds investment specifically in downturns rather than at all times.

Applying the -0.66 user-cost elasticity to the measured change in the user cost of capital following the 1962 reform implies the aggregate equipment investment-capital ratio should have risen by about 0.01, or roughly 7 percent – corresponding to about $7 billion in 1987 prices – compared with an actual observed rise of 0.017, or about 11 percent. The authors are careful to bound the importance of this channel: the standard deviation of the investment-capital ratio over their full sample is 0.038, “roughly four times the mean predicted effect of the major tax reforms,” so while they conclude “a strong case can be made that [tax parameters] are important,” they are explicit that tax changes are only one piece of a puzzle in which interest rates, productivity, and capital-goods prices also move investment, and that isolating those other channels with similarly clean identification is likely to be harder.

The authors test two implications of Dixit-and-Pindyck-style irreversibility models: that anticipated reforms should cause visible “bunching” of investment timed around the policy switch, and that estimated tax-variable coefficients should differ systematically depending on whether a reform makes tax treatment more or less generous. Examining transition patterns in investment rates around the Tax Reform Act of 1986 (and, by the authors’ account, the other major reforms), they find “no discernible bunching,” and they note the estimated coefficients are “quite similar” in 1982 and 1987 even though investment tax policy moved in opposite directions in those two episodes – leading them to conclude that “we do not believe that our results necessarily favor” irreversibility-based models over the neoclassical convex-adjustment-cost framework, while acknowledging that developing sharper tests to distinguish the two remains an open task.