Returns to Scale in U.S. Production: Estimates and Implications

The authors motivate the question by noting that “some models offer predictions that differ significantly from those of more standard models only with substantial increasing returns and a high degree of imperfect competition,” so assessing the data’s actual magnitude of returns to scale is necessary “in assessing the merits of these models.” They cite work in which countercyclical markups let government-spending shocks raise real wages, work in which increasing returns amplify measured productivity responses to shocks, and – “perhaps most strikingly” – work in which sufficiently large increasing returns generate multiple equilibria driven by sunspots or purely nominal shocks (citing Rotemberg and Woodford 1992, Farmer and Guo 1994, and Beaudry and Devereux 1994).

At the firm level, the paper writes gross output as Y = F(K, L, M, T) and shows that cost minimization implies the growth rate of output equals returns to scale γ times the cost-share-weighted growth rate of inputs, plus technology growth – “this equation generalizes Hall’s (1990, equation 5.29)” generalization of the Solow residual to allow for non-constant returns and profits. The paper derives the identity γ = AC/MC = (P/MC)(AC/P) = μ(1 − s_π), linking returns to scale to the price-cost markup μ and the profit share s_π; since the authors “estimate an average profit rate of at most 3 percent,” they conclude μ “approximately equals” γ, so large measured increasing or decreasing returns map directly into economically implausible markups if taken as structural. The paper explicitly notes that, because strongly decreasing returns combined with low observed profits would imply firms persistently pricing below marginal cost – which “makes no economic sense” – the authors “believe a priori that returns to scale should be no lower than constant.”

The paper shows that value added is “not a natural measure of output” and “can in general only be interpreted as such with perfect competition”; under imperfect competition, using value added (even at the firm level) “suffers from an omitted variable bias,” captured by an extra term in equation (7) involving the gap between materials growth and output growth (dm − dy). This omitted term is identically zero only under perfect competition or a zero elasticity of substitution between materials and other inputs; otherwise its sign depends on the covariance between materials intensity and the business cycle, and the paper notes that “if materials intensity is procyclical, the bias is positive.” The paper further derives (equation 10) the mapping between gross-output returns to scale γ and the corresponding value-added-equivalent parameter γ^V, used throughout to make the two measures comparable.

The paper uses Dale Jorgenson’s dataset for 34 industries constituting the U.S. private business economy, 1959-89, which Jorgenson, Gollop and Fraumeni (1987) “document thoroughly” and which the authors describe as “a massive effort to ensure consistency with production theory,” covering primary and intermediate inputs as well as gross output. Following Hall (1990), they consider both OLS and instrumental-variables (2SLS) regressions using changes in the world oil price, government defense spending, and the political party of the president as demand-side instruments, but ultimately “emphasize the uninstrumented results” because, among other reasons, the paper’s own Section III shows that such demand-side instruments “need not be uncorrelated with reallocation effects, and hence may be invalid” – a point later verified empirically (Q9) by regressing the paper’s own aggregation-correction terms on these instruments and finding significant correlations.

The first puzzle is that “estimated returns to scale are strikingly larger in aggregate than in industry-level data”: instrumented, the value-added-equivalent γ^V for the entire private economy is 1.72 and for durables manufacturing is 1.46 – both “large enough to justify some existing models of multiple equilibria” – whereas the weighted average of the 34 individual industry-level estimates shows only durable-goods manufacturing with any evidence of increasing returns at all, and there with a point estimate of just γ^V = 1.28. The uninstrumented point estimates are, for the most part, “little changed,” with standard errors affected the most; uninstrumented, constant returns can now be rejected at the 1 percent level for total manufacturing gross output.

The second puzzle is that the weighted average of individual-industry estimates is “strongly diminishing” in some cases – “for manufacturing overall, the typical industry has diminishing returns to gross output” – and the paper stresses that strongly diminishing firm-level returns, combined with the small observed profit rates in the data, would imply firms “consistently price output below marginal cost, which obviously makes no economic sense.” Five individual industry estimates are significantly less than one at the 5 percent level, versus three significantly greater than one, with an average γ^V of 1.16 for the whole private economy but a median of just 1.01 across industries – so “half the estimates are less than one.”

The third puzzle is that value-added point estimates are “consistently smaller” than the implied γ^V from gross-output estimates, with standard errors large enough that constant returns can never be rejected in the instrumented value-added regressions; the most striking case is manufacturing non-durables, where “the point estimate suggests returns to scale of about zero.” The paper explicitly checks whether the omitted-variable-bias mechanism from equation (7) explains this: since the markup is assumed ≥ 1, that mechanism predicts value-added estimates should be biased upward relative to gross-output estimates, and the estimated bias coefficient is indeed positive for 22 of the 34 industries (averaging about 0.1) as well as for all aggregates – “thus, the firm-level theory that predicts differences between these two estimates does not explain the differences we actually find” empirically, since value-added estimates are in fact smaller, not larger.

The paper decomposes aggregate gross-output growth as dy = γ̄·dx + R + dt, where γ̄ is the weighted-average firm-level returns to scale, dt is weighted-average technology growth, and R = Σwᵢ(γᵢ − γ̄)·dxᵢ is a “reallocation” term that “contributes positively to growth if firms with high returns to scale have higher-than-average growth in inputs” – formally, defining a “cyclicality” parameter βᵢ as the regression coefficient of firm-level input growth dxᵢ on aggregate input growth dx, the OLS bias from omitting R is positive whenever a firm’s own γᵢ is positively correlated with its βᵢ. An analogous reallocation term R^V, plus an additional term I capturing cyclical variation in materials intensity, applies to value-added growth. The authors argue this single mechanism can explain all three puzzles: if durable-goods industries (which the paper separately documents have both higher returns to scale and more procyclical output) see disproportionate input growth in booms, that reallocation alone can make aggregates look like they have stronger increasing returns than any individual firm does, can make some industries’ own within-industry reallocation look like decreasing returns, and can affect gross-output and value-added data differently since the two reallocation terms (R and R^V/I) need not be numerically equal.

The authors estimate the reallocation terms R, R^V and I directly from the sectoral returns-to-scale estimates and subtract them from actual aggregate growth before re-regressing on aggregate input growth, reporting the results (Table 3) as returns to scale “corrected for reallocations.” The results “suggest constant returns” for the private economy as a whole (gross output γ = 1.01, implied value-added γ^V = 1.02, direct value-added estimate 1.03 – all three measures now close together, unlike the uncorrected Table 1/2 results), with manufacturing durables still showing statistically significant mild increasing returns (1.11-1.36 depending on measure) and non-durables mild, not-statistically-significant decreasing returns (0.81-0.96). Critically, “nowhere in Table 3 do we have the puzzle of statistically significant decreasing returns” – the troubling second puzzle disappears entirely once aggregation is corrected for.

No – “the results in Table 3 show that correcting for aggregation does not recover industry-level averages from aggregate data,” and the authors are explicit that without firm-level data “we cannot be certain” the Table 3 estimates are unbiased, though they “suggest the factors that matter.” Using a heuristic decomposition (equations 18-20) of how within-industry (firm-to-industry) reallocation could bias even the industry-level Table 2 estimates, the authors argue their priors favor the corrected Table 3 estimates as closer to the true average firm-level parameter, based on three pieces of evidence: Table 2’s own value-added/gross-output gap implies an economically necessary negative bias parameter; the paper’s own aggregate reallocation term is estimated to be procyclical; and the estimated firm-level cyclicality parameters show little correlation with the potential source of remaining bias, so that residual bias is “probably small.” They nonetheless frame the choice between Table 2 and Table 3 as ultimately “an economic question” about which estimate better captures the true forces at work in business cycles, not one resolved definitively by the data alone.

Using a stylized model (a single représentative firm with multiple, Pareto-ranked, Cooper-and-Jöhn-style equilibria under sufficiently strong increasing returns, versus a two-firm heterogeneous economy with constant-returns technologies at the firm level), the paper shows there is “no general answer” to whether it is safe to calibrate a one-sector macro model using aggregate data while ignoring underlying heterogeneity: “in one case, it is safe to ignore heterogeneity… But in another case, this procedure is misleading,” and “interestingly, the appropriate procedure depends on non-production institutions in the economy.” In the two-firm example, reallocation across heterogeneous constant-returns firms can itself generate the same kind of multiple, Pareto-ranked equilibria that would otherwise require implausibly large increasing returns in a representative-firm model – but whether it does so depends on features like how labor markets allocate workers across the two firms, not on the production technology alone. The authors conclude that the empirical finding of approximately constant firm-level returns to scale “does not necessarily allow us to reject macroeconomic parables in which increasing returns at a representative firm play a central role,” since reallocation effects can substitute for genuine firm-level increasing returns in generating similar aggregate phenomena.

The paper directly engages Caballero and Lyons (1992), who “first noted the puzzle that returns to scale rise at higher levels of aggregation” and interpreted it as evidence of “enormous productive spillovers across industries,” and counters that “we do not find their explanation compelling” because, among other reasons, Basu and Fernald (1995a) found the Caballero-Lyons specification “shows apparent externalities in value-added data, but not in gross-output data,” which “true productive spillovers” should not produce. The paper separately argues that cyclical variation in capacity utilization – a popular alternative explanation for procyclical measured productivity – “cannot… explain our three puzzles,” since (i) utilization stories explain apparent increasing, not decreasing, returns; (ii) they cannot explain why industry- and aggregate-level estimates differ, since if utilization inflates apparent returns at the industry level it should do so equally at the aggregate level; and (iii) utilization affects value-added and gross-output regressions in the same direction, so it cannot explain the paper’s third (gross-output-versus-value-added) puzzle.