Disagreement Among Firm-Level Productivity Estimators and Its Consequences for Applied Inference

Abstract

Firm-level total factor productivity is not observed: it is estimated, and an applied regression inherits that choice. We give four elementary propositions on the two measurement errors involved. On the left-hand side, the gap between any two residual-based measures in a downstream regression has a closed form in their implied factor elasticities. On the right-hand side, attenuation depends on the reliability of the variation that the estimator uses, and a two-rating design is exactly identified, so its uncorrelated-errors assumption has no testable implication. The propositions are applied to 29,434 firm-years across 4517 Chinese A-share firms (2015–2024) and to eleven measures: six parametric production-function estimators and five nonparametric frontier measures. The closed form predicts the realised gaps among the parametric measures with a correlation of 1.000. Under one specification, the six parametric measures give a positive ESG coefficient, significant at 1 percent, and the five nonparametric measures a coefficient indistinguishable from zero. The nonparametric measures penalise undesirable outputs, so the contrast is not estimator disagreement alone. A conventional slacks-based score on the same inputs and revenue, without those outputs, ranks with the baseline parametric measure at 0.70 rather than 0.23, and its ESG coefficient is positive.

1. Introduction

Total factor productivity is a residual. It is what remains of output after the contributions of measured inputs have been removed, which means it is defined only relative to an assumed production technology and an estimation procedure for that technology. It is also, as Syverson [1] observes in surveying what is known about it, a quantity whose measured dispersion across firms is large enough that explaining it has become a literature in its own right—which makes how it is measured a question of some consequence. Two types of literature have developed procedures for the task and have largely proceeded in parallel. The parametric literature specifies a production function and confronts the simultaneity between input choices and unobserved productivity, from the proxy-variable estimators of Olley and Pakes [2] and Levinsohn and Petrin [3] through the refinements of Ackerberg, Caves, and Frazer [4]. The nonparametric literature constructs a frontier directly by mathematical programming and measures productivity as the distance to it, using data envelopment analysis and, where undesirable outputs matter, slacks-based directional distance functions and the Malmquist–Luenberger index [5,6]. Wooldridge [7] recasts the two-stage proxy-variable procedure as a single-equation GMM system, joining Olley and Pakes, Levinsohn and Petrin, and Ackerberg, Caves and Frazer as a fourth standard member of the identifying-assumption family; we retain the original two-stage form throughout because it is the version already implemented for the five parametric measures in the panel.

Applied researchers choose one procedure, report a robustness check under one or two alternatives from the same family and proceed. This paper asks what that practice conceals. We construct eleven productivity measures for the same firms over the same period and compare them on four dimensions: the levels they assign, the rankings they imply, how they allocate variance between and within firms, and—most consequentially—the answer they give when used as the dependent variable in an identical applied regression. Three questions organise what follows. Within the parametric family, how large is the disagreement in levels, ranks and downstream coefficients, and does the closed form of Proposition 1 account for it? Once nonparametric measures that price undesirable outputs are set beside residual-based measures, how much of the remaining disagreement is a difference of construct rather than of estimator? And, where the technology is known, which estimators stay close to the truth as the permanent firm component of productivity grows?

Three literatures bear on the exercise, and they have largely run in parallel. The first is the identification of production functions, which since Olley and Pakes [2] and Levinsohn and Petrin [3] has concentrated on recovering factor elasticities consistently in the presence of a productivity shock the firm observes and the econometrician does not; Ackerberg, Caves and Frazer [4] repaired the functional dependence in the first stage, and Gandhi, Navarro and Rivers [8] showed that gross-output specifications are not identified from the timing assumptions alone and supplied the additional restriction that identifies them. Bond, Hashemi, Kaplan and Zoch [9] are closest in spirit to what follows: they show that elasticity estimates recovered from revenue data are fragile in ways that propagate to the objects built on them. That literature asks how to get the technology right. It does not ask what happens downstream when one does not. The comparison exercise that follows has a direct methodological precedent in Van Biesebroeck [10], who compares index-number, data-envelopment, stochastic-frontier, GMM and semiparametric productivity estimators under simulated measurement error and factor-price heterogeneity; what is added here is the downstream applied regression, the nonparametric SBM/Malmquist–Luenberger family, the ESG-rating measurement-error analysis, and the Chinese listed-firm setting.

The second is the econometrics of measurement error, surveyed by Schennach [11], whose panel-data branch begins with Griliches and Hausman [12] and whose treatment of nonclassical error runs through Black, Berger and Scott [13] and Hu and Schennach [14]. The design used here to recover rating reliability—two noisy indicators of one latent quantity, each instrumenting the other—is the one Ashenfelter and Krueger [15] applied to twins’ reports of schooling. That literature has said a great deal about error in regressors and comparatively little about error in a dependent variable that is itself an estimated residual.

The third is the measurement of ESG itself. Berg, Kölbel and Rigobon [16] established that the major rating agencies disagree substantially, decomposing the divergence into differences of scope, measurement and weighting; Christensen, Serafeim and Sikochi [17] show that disagreement rises with disclosure rather than falling with it. Li and Chen [18] offer a competing reading, reporting that disagreement improves analyst forecast accuracy by attracting attention rather than degrading it—an information rather than a noise account. That work characterises the disagreement. It does not trace what the disagreement does to an applied coefficient, which is the question here.

What this paper adds is the connection between the disagreement and its effect on an applied coefficient. Both sides of the regression are estimated, and the two errors have different structures: on the left, a deterministic consequence of an assumed technology, and on the right, a stochastic error in an indicator. Section 3 treats them together and reports four results. Proposition 1 gives a closed-form expression for the gap between any two residual-based measures in a downstream regression—a quantity that is arithmetic rather than statistical, and that we have not found stated. Proposition 2 and Corollary 2 sharpen the Griliches–Hausman observation that differencing worsens attenuation into a necessary and sufficient condition in variance components. Proposition 3 and Corollary 3 give the estimand of the two-rating instrumental-variables design and the exact factor by which it falls short when the raters’ errors are correlated, in the bounding tradition of Black, Berger and Scott. Proposition 4 shows that the design is exactly identified, so that its own identifying assumption has no testable implication—a limitation the applied literature invoking this design does not appear to note.

The results are ordered by how much they should worry an applied researcher. Within the parametric family, the measures agree on ordering but not on level, and the disagreement is large enough to reclassify a third of firm-years across productivity quartiles. Across families, agreement essentially vanishes. And in a downstream application, the two families do not merely differ in magnitude: one yields a uniformly significant positive association and the other a uniformly insignificant one, on overlapping firms and years, with the same controls. Section 5.7 records that the samples are not identical and that the contrast is not a test of coefficient equality. We therefore do not read a low correlation, or a change of significance, across the two families as evidence that one estimator of a common object has failed.

We are explicit about what this does and does not show. The two families are not competing estimators of one object. The nonparametric measures used here price undesirable outputs and therefore capture environmental as well as technical performance; low agreement with revenue-based parametric TFP is expected in part. The contribution is to quantify how far apart they are and to show that a literature which cites both as evidence about “productivity” is aggregating results that do not aggregate.

2. Two Families of Productivity Measurement

2.1. Parametric Production-Function Estimation

Write output in logs as y = β_ll + β_kk + ω + ε, where ω is productivity known to the firm when inputs are chosen and ε is measurement error or an ex post shock. Ordinary least squares is inconsistent because input choices respond to ω. Within-firm fixed effects remove any time-invariant component of ω but not its evolution. System GMM instruments differenced inputs with lagged levels under a Markov restriction on ω. The proxy-variable estimators invert a monotone input demand to recover ω: Olley and Pakes [2] use investment, and Levinsohn and Petrin [3] use intermediate inputs, thereby avoiding the exclusion of the zero-investment observations that the investment proxy requires. All six estimators used here target the same object and differ only in the identifying assumption used to reach it.

2.2. Nonparametric Frontier Measurement

The nonparametric approach makes no functional-form assumption. A best-practice frontier is constructed by linear programming over the observed input–output combinations, and a firm’s productivity is its distance to that frontier; Emrouznejad and Yang [19] count more than ten thousand studies in this tradition over its first four decades. The slacks-based measure of Tone [6] accommodates non-radial slack in individual inputs and outputs; the directional distance function of Chung, Färe, and Grosskopf [5] allows desirable outputs to expand while undesirable outputs contract, which is what makes the approach natural when emissions are part of the production set. The Malmquist–Luenberger index chains these distances over time and decomposes productivity change into efficiency change (movement toward the frontier) and technical change (movement of the frontier itself).

Formally, let n decision-making units each use m inputs x ∈ ℝ₊^m to produce s₁ desirable outputs y jointly with s₂ undesirable outputs b. The production possibility set is spanned by the observed units,

T = {(x, y, b): Σ_j λ_j x_j ≤ x, Σ_j λ_j y_j ≥ y, Σ_j λ_j b_j = b, λ ≥ 0, Σ_j λ_j = 1},

(1)

where the equality on b imposes weak disposability—undesirable outputs cannot be discarded without cost—and the adding-up constraint on λ imposes variable returns to scale. In the measures used here, m = 2 (labour and capital), s₁ = 1 (revenue), and s₂ = 2 (sulphur dioxide and chemical oxygen demand), with nitrogen oxides and particulates added in a robustness variant.

Slacks-based efficiency. For unit o, the slacks-based measure of Tone [6], extended to undesirable outputs, solves the fractional program

ρ*_o = min [1 − (1/m) Σ_i s_i⁻/x_io]/[1 + (1/(s₁ + s₂)) (Σ_r s_r^g/y_ro + Σ_t s_t^b/b_to)]

(2)

subject to x_io = Σ_j λ_j x_ij + s_i⁻, y_ro = Σ_j λ_j y_rj − s_r^g, b_to = Σ_j λ_j b_tj + s_t^b, with λ, s⁻, s^g, s^b ≥ 0 and Σ_j λ_j = 1. The measure is non-oriented: it charges for input excess and output shortfall simultaneously, and ρ*_o ∈ (0, 1] attains unity only when every slack vanishes.

Program (2) is fractional rather than linear. The Charnes–Cooper [20] transformation removes the ratio: introducing a scalar t > 0 and setting Λ = tλ, S⁻ = ts⁻, S^g = ts^g, and S^b = ts^b gives the linear program

min t − (1/m) Σ_i S_i⁻/x_io

(3)

subject to t + (1/(s₁ + s₂)) (Σ_r S_r^g/y_ro + Σ_t S_t^b/b_to) = 1, t x_io − Σ_j Λ_j x_ij − S_i⁻ = 0, t y_ro − Σ_j Λ_j y_rj + S_r^g = 0, t b_to − Σ_j Λ_j b_tj − S_t^b = 0, Σ_j Λ_j − t = 0, Λ ≥ 0, S ≥ 0, whose optimal value equals ρ*_o. One such program is solved per firm-year against the contemporaneous frontier.

Directional distance and the Malmquist–Luenberger index. The directional distance function of Chung, Färe, and Grosskopf [5], taken in the direction g = (y_o, −b_o), expands desirable output and contracts undesirable output in the same proportion:

D(x_o, y_o, b_o) = max β

subject to Σ_j λ_j x_ij ≤ x_io, Σ_j λ_j y_rj ≥ (1 + β) y_ro, Σ_j λ_j b_tj = (1 − β) b_to, λ ≥ 0, Σ_j λ_j = 1, β ≥ 0

(4)

Write D^t for (4) solved against the frontier spanned by period-t observations and D^G for the same program solved against the global frontier spanned by every period [21]. The global Malmquist–Luenberger index between t and t + 1, and its decomposition, are

GML = (1 + D^G_t)/(1 + D^G_t+1), EC = (1 + D^t_t)/(1 + D^t+1_t+1), TC = GML/EC

(5)

A value of GML above unity signals productivity growth; EC attributes it to movement toward the frontier and TC to movement of the frontier itself. The global reference set makes the index circular and avoids the infeasibilities that afflict the adjacent-period formulation. Chaining GML from a base year normalised to unity gives a cumulative level index.

Three programs are therefore solved for each firm-year of the 2016–2023 panel—one contemporaneous slacks-based program (3), one contemporaneous directional distance program (4) and one global directional distance program—yielding the five nonparametric measures compared below: the slacks-based score, its cumulative level and the index GML with its two components, EC and TC. Input and output columns are rescaled to unit sample mean before solving, which improves conditioning without altering ρ* or β, both of which are ratios. Read in order, the objects are nested rather than parallel. Equation (2) is the slacks-based score. Equation (3) is that same score after the Charnes–Cooper transformation, and it is (3), not (2), that is solved once per firm-year against the contemporaneous frontier; the SBM level is those scores chained from a base year. Equation (4) is a different distance, a proportional expansion of desirable output and contraction of undesirable output. Equation (5) does not estimate another technology: it forms the Malmquist–Luenberger index and its efficiency-change component as ratios of distances from (4) and defines technical change as the quotient of those two ratios. The five nonparametric measures are therefore one slacks-based score, its level and three transformations of the directional distance.

3. A Two-Sided Measurement Problem

Both sides of the regression that motivates this paper are estimated rather than observed. On the left, a productivity measure is a residual whose value depends on an assumed technology. On the right, an ESG rating is one agency’s reading of a construct no agency observes. This section states what each kind of measurement error implies for the applied estimand, and what the data can and cannot reveal about it. The proofs are elementary and are given in full because the results are used to interpret Section 5.

3.1. Notation and a Preliminary Lemma

Every regression in this paper has the same shape. A variable v is projected on the regressor of interest s, a control vector w, a full set of firm effects and a full set of year effects. Collect everything other than s in a matrix Z, so that Z holds the controls and the two sets of dummies, and let M = I − Z(Z′Z)⁻Z′ be the projection onto the orthogonal complement of the column space of Z, with (·)⁻ a generalised inverse. By the Frisch–Waugh–Lovell theorem, the coefficient on s in the regression of v on (s, Z) is

b(v) = (s′Ms)⁻¹ s′Mv

(6)

Lemma 1. 

Fix the design matrix, so that s and Z—and hence M—are held fixed, and suppose s′Ms > 0. Then, the map v ↦ b(v) defined by (6) is a linear functional on ℝⁿ: for any vectors v₁, v₂ and any scalars c₁, c₂,

b(c₁v₁ + c₂v₂) = c₁ b(v₁) + c₂ b(v₂), and b(Zc) = 0 for every conformable c.

Proof. 

Linearity is immediate from (6), since v enters only through the linear expression s′Mv: b(c₁v₁ + c₂v₂) = (s′Ms)⁻¹ s′M(c₁v₁ + c₂v₂) = c₁(s′Ms)⁻¹s′Mv₁ + c₂(s′Ms)⁻¹s′Mv₂. For the second claim, M annihilates the column space of Z by construction, so MZc = 0 and therefore b(Zc) = 0. In particular, b annihilates the intercept, the controls and any variable that is constant within a firm or within a year. □

Two features of Lemma 1 are used repeatedly. Linearity means that the coefficient attached to a sum of variables is the sum of the coefficients attached to each, and the annihilation property means that anything absorbed by the design contributes nothing. Neither requires any assumption about how the data were generated: (6) is an algebraic identity for a given sample, so the results of this section hold in finite samples and are not asymptotic approximations.

3.2. The Dependent-Variable Side

Let two productivity measures be residuals from Cobb–Douglas production functions that share an output series but differ in the factor elasticities they impose:

m^A = y − β_l^A l − β_k^A k,  m^B = y − β_l^B l − β_k^B k

(7)

Nothing is assumed about where β_l^A, β_k^A, β_l^B, and β_k^B come from. They may be the output of any estimator, consistent or not, and they may be recovered after the fact from a supplied measure in the manner of Section 5.3. That they differ across estimators is not in doubt: Gandhi, Navarro and Rivers [8] show that the gross-output case is not identified without a restriction beyond the timing assumptions, and Bond, Hashemi, Kaplan and Zoch [9] document how far apart the resulting elasticities can be. What follows takes that dispersion as given and asks what it costs.

Proposition 1. 

Let Δβ_l = β_l^B − β_l^A and Δβ_k = β_k^B − β_k^A. Then:

(i) m^A − m^B = Δβ_l l + Δβ_k k, a deterministic function of the measured inputs alone;

(ii) writing β^{^A} = b(m^A) and β^{^B} = b(m^B) for the coefficients on s obtained from identical specifications, and γ_l = b(l), γ_k = b(k),

β^{^A} − β^{^B} = Δβ_l γ_l + Δβ_k γ_k;

(8) 

(iii) if instead the two measures are residuals from a function with J factors x₁, …, x_j, so that m^A = y − Σ_j β_j^A x_j and likewise for B, then β^{^A} − β^B = Σ_j Δβ_j γ_j with Δβ_j = β_j^B − β_j^A and γ_j = b(x_j).

Proof. 

(i) Subtract the two expressions in (7). The output series y appears once in each with coefficient one and cancels, leaving m^A − m^B = (β_l^B − β_l^A) l + (β_k^B − β_k^A) k = Δβ_l l + Δβ_k k. No disturbance appears on the right-hand side: whatever stochastic component the two measures carry, they carry the same one, and it is differenced away.

(ii) Both coefficients are produced by the same specification, so the same Z, the same M and the same s enter each, and Lemma 1 applies with b held fixed across the two. By linearity, β^{^A} − β^{^B} = b(m^A) − b(m^B) = b(m^A − m^B). Substituting part (i) and applying linearity once more, b(Δβ_l l + Δβ_k k) = Δβ_l b(l) + Δβ_k b(k) = Δβ_l γ_l + Δβ_k γ_k, which is (8).

(iii) Identical, with the two-term sum replaced by a sum over j: part (i) gives m^A − m^B = Σ_j Δβ_j x_j, and J applications of linearity give the stated expression. □

Corollary 1. 

Write Δβ = (Δβ_l, Δβ_k)′ and γ = (γ_l, γ_k)′. Then |β^{^A} − β^{^B}| ≤ ‖Δβ‖ ‖γ‖, with equality when the two vectors are parallel. In particular, if γ = 0—the regressor is orthogonal to every input once the controls and effects are partialled out—then every residual-based measure delivers the same coefficient, however far apart the technologies they impose.

Proof. 

Equation (8) states that β^{^A} − β^{^B} is the inner product Δβ′γ; the bound is Cauchy–Schwarz, and the equality case is its equality case. If γ = 0, the inner product vanishes for any Δβ. □

Two consequences deserve emphasis. First, the gap in (8) is deterministic given the design and the two elasticity vectors. It contains no disturbance, it does not shrink as the sample grows, and no resampling scheme will reveal it because it is not sampling variation. A robustness check that substitutes one residual-based measure for another therefore does not probe the stability of an estimate in the usual sense; it evaluates a different estimand, displaced by a quantity that Proposition 1 computes exactly.

Second, Corollary 1 identifies what governs the size of the displacement. It is large when the measures assume very different technologies and the regressor is strongly associated with the inputs, and it is zero when either factor is absent. This is checkable before any measure is chosen: γ_l and γ_k are obtained from two auxiliary regressions of the inputs on the regressor, and the implied elasticities can be recovered from any supplied measure by the exercise of Section 5.3.

3.3. The Regressor Side

Turn to the other side of the same regression. Let ξ denote a latent construct—the environmental, social and governance conduct that ratings attempt to score—and let agency j report an indicator

s_j = λ_j ξ + e_j, E[e_j ξ] = 0, E[e₁ e₂] = 0,

(9)

with the outcome generated by y = βξ + u, where E[uξ] = 0 and E[u e_j] = 0. All variables are taken as residuals after the partialling-out procedure described in Section 3.1 and are normalised so that Var(ξ) = 1 and Var(s_j) = 1. Under this normalisation, Var(s_j) = λ²_j Var(ξ) + Var(e_j) = λ²_j + Var(e_j) = 1, so λ²_j is exactly the reliability of agency j’s rating: the share of its variance attributable to the construct rather than to the agency’s error.

Proposition 2 (attenuation). 

Under (9), the least-squares projection of y on s_j has probability limit βλ_j. The estimand is therefore attenuated towards zero by the factor λ_j = √(reliability). Moreover, decomposing each of ξ and e_j into between-firm and within-firm components with variances σ²_{ξ,b}, σ²_{ξ,w} and σ²_{e,b}, σ²_{e,w}, the pooled and within-firm reliabilities are

r^p = λ²(σ²_{ξ,b} + σ²_{ξ,w})/[λ²(σ²_{ξ,b} + σ²_{ξ,w}) + σ²_{e,b} + σ²_{e,w}],

r^w = λ²σ²_{ξ,w}/[λ²σ²_{ξ,w} + σ²_{e,w}]

(10) 

Proof. 

Since Var(s_j) = 1, the projection coefficient equals the covariance: Cov(y, s_j) = Cov(βξ + u, λ_jξ + e_j) = βλ_j Var(ξ) + β E[ξ e_j] + λ_j E[uξ] + E[u e_j] = βλ_j, the last three terms vanishing by the orthogonality conditions in (9) and the assumptions on u. Since λ²_j is the reliability, λ_j is its square root, which is the stated attenuation factor. The expressions in (10) follow from applying the definition of reliability to the pooled variance and to the within-firm variance, respectively, the two components being orthogonal by construction of the within transformation. □

Corollary 2. 

r^w < r^p if and only if σ²_{ξ,b}/σ²_{ξ,w} > σ²_{e,b}/σ²_{e,w}; that is, if and only if the construct is relatively more of a between-firm attribute than the agency’s error is. The two reliabilities coincide when the ratios are equal.

Proof. 

Both denominators in (10) are positive, so the inequality r^w < r^p may be cross-multiplied. Writing the four variances as ξ_b, ξ_w, e_b, e_w for brevity and cancelling λ² from both sides, the inequality becomes ξ_w[λ²(ξ_b + ξ_w) + e_b + e_w] < (ξ_b + ξ_w)[λ²ξ_w + e_w]. Expanding both sides gives λ²ξ_wξ_b + λ²ξ_w² + ξ_w e_b + ξ_w e_w on the left and λ²ξ_bξ_w + λ²ξ_w² + ξ_b e_w + ξ_w e_w on the right. The three terms λ²ξ_bξ_w, λ²ξ_w² and ξ_w e_w appear on both sides and cancel, leaving ξ_w e_b < ξ_b e_w, which upon dividing by ξ_w e_w > 0 is ξ_b/ξ_w > e_b/e_w. □

That differencing or demeaning aggravates attenuation is the observation of Griliches and Hausman [12], who noted that the within transformation removes signal faster than noise when the signal is the more persistent of the two; Corollary 2 states the condition under which this happens and shows it to be necessary as well as sufficient. Corollary 2 also explains why the reduction documented in Section 5.9 is to be expected rather than anomalous. A rating is largely a statement about the kind of firm under assessment, so its signal is heavily cross-sectional; the agency’s idiosyncratic error, by contrast, has no particular reason to be persistent. A within-firm design discards the component in which the signal is concentrated and retains the component in which the error is, which is precisely the configuration under which r^w < r^p.

The design of Proposition 3 is the one Ashenfelter and Krueger [15] used on twins’ reports of schooling, and it is the workhorse of the applied literature whenever a second reading of the same latent quantity is available.

Proposition 3 (errors-in-variables instrumental variables). 

Under (9), and provided Cov(s_j, s_k) = λ_jλ_k ≠ 0, instrumenting s_j with s_k for k ≠ j has probability limit β/λ_j. Consequently the ratio of the instrumented to the uninstrumented coefficient is

R_j = (β/λ_j)/(βλ_j) = 1/λ²_j,

the reciprocal of agency j’s reliability, which is free of β and therefore estimable without knowing the parameter of interest.

Proof. 

The just-identified instrumental-variables estimand is the ratio of the covariance of the outcome with the instrument to the covariance of the regressor with the instrument. The numerator is Cov(y, s_k) = Cov(βξ + u, λ_kξ + e_k) = βλ_k, by the same cancellations as in Proposition 2. The denominator is Cov(s_j, s_k) = Cov(λ_jξ + e_j, λ_kξ + e_k) = λ_jλ_k + E[e_j e_k] = λ_jλ_k, the error covariance vanishing by the third condition in (9). The ratio is βλ_k/(λ_jλ_k) = β/λ_j, which requires λ_k ≠ 0 for the cancellation and λ_j ≠ 0 for the quotient. Dividing by the limit βλ_j established in Proposition 2 gives R_j = 1/λ²_j. □

Corollary 3 (what a correlated error costs). 

Suppose the third condition in (9) fails, so that E[e₁e₂] = σ₁₂ ≠ 0 while the remaining assumptions hold. Then instrumenting s_j with s_k has probability limit

βλ_k/(λ₁λ₂ + σ₁₂) = (β/λ_j)·[1 + σ₁₂/(λ₁λ₂)]⁻¹

(11) 

The instrumental-variables estimator therefore removes only part of the attenuation when σ₁₂ > 0 and overcorrects when σ₁₂ < 0. Two agencies reading the same corporate disclosures are the leading case of σ₁₂ > 0, under which the corrected estimate remains attenuated, so the design is conservative in the direction that matters. Deriving what can still be said when the classical assumption fails, rather than abandoning the estimator, follows Black, Berger and Scott [13] and the nonclassical measurement-error literature more generally [11,14].

Proof. 

The numerator of the estimand is unchanged at βλ_k. The denominator becomes Cov(s_j, s_k) = λ_jλ_k + σ₁₂, since the error covariance no longer vanishes. Dividing the numerator by the denominator and factoring λ₁λ₂ out of the denominator gives (11). The sign statements follow because [1 + σ₁₂/(λ₁λ₂)]⁻¹ is smaller than one when σ₁₂ and λ₁λ₂ share a sign and larger than one when they do not. □

Proposition 4 (separate identification and its limit). 

Write ρ = E[s₁s₂], n₁ = E[y s₁] and n₂ = E[y s₂] and suppose ρ ≠ 0 and n₂ ≠ 0. Then:

(i) The three unknowns (λ₁, λ₂, β) are exactly identified from (ρ, n₁, n₂), up to a common change of sign, by

λ²₁ = ρ n₁/n₂, λ²₂ = ρ n₂/n₁, β = n₁/λ₁;

(12) 

in particular, the two reliabilities are recovered separately, with no assumption that the agencies are equally reliable;

(ii) The system carries no over-identifying restriction. Writing R₁ and R₂ for the two ratios of Proposition 3, R₁R₂ = 1/ρ² holds identically, for any data whatsoever. The assumption E[e₁e₂] = 0 therefore has no testable implication within this design.

Proof. 

(i) The three moments implied by (9) and the outcome equation are ρ = Cov(s₁, s₂) = λ₁λ₂, n₁ = Cov(y, s₁) = βλ₁ and n₂ = Cov(y, s₂) = βλ₂, the cancellations being those of Proposition 2. Since n₂ ≠ 0, the ratio n₁/n₂ = βλ₁/(βλ₂) = λ₁/λ₂ is well defined and identifies the ratio of the loadings; β cancels, so no knowledge of the parameter of interest is required at this step. Multiplying by ρ = λ₁λ₂ gives ρ (n₁/n₂) = λ₁λ₂·λ₁/λ₂ = λ²₁, and symmetrically ρ (n₂/n₁) = λ²₂. Taking either square root and substituting into n₁ = βλ₁ yields β. The sign indeterminacy is genuine and unavoidable: replacing (λ₁, λ₂, β) by (−λ₁, −λ₂, −β) leaves ρ, n₁ and n₂ unchanged, so the sign must be fixed by convention, for instance by requiring λ₁ > 0, which amounts to orienting the latent construct so that the first agency scores it positively. Three equations in three unknowns with a unique solution up to that convention constitute exact identification.

(ii) Substituting the estimands of Proposition 3 in terms of the moments, the instrumented coefficients are iv₁ = n₂/ρ and iv₂ = n₁/ρ, while the uninstrumented ones are n₁ and n₂. Hence R₁ = iv₁/n₁ = n₂/(ρn₁) and R₂ = iv₂/n₂ = n₁/(ρn₂), so that

R₁R₂ = [n₂/(ρn₁)]·[n₁/(ρn₂)] = 1/ρ²,

in which n₁ and n₂ cancel entirely. The relation therefore holds as an algebraic identity in the sample moments and carries no information about whether (9) is true. Equivalently: three moments determine three unknowns with no degree of freedom left over, and a restriction that consumes no degree of freedom cannot be violated by data. □

Part (ii) is worth stating plainly because the two-rating instrumental-variables design is common in applied work on ESG ratings and its identifying assumption is often discussed as though the data bore on it. They do not. The observed indicator correlation and the value implied by the two ratios will agree exactly, on any data whatsoever, and this agreement is not evidence. What Corollary 3 adds is that the cost of the assumption failing is nonetheless computable: the correction is short of the mark by the factor [1 + σ₁₂/(λ₁λ₂)]⁻¹, so a researcher willing to bound σ₁₂ can bound the residual attenuation even without being able to test for it.

Remark 1. 

A third indicator restores testability. With three ratings, the loadings and β number four, while the observable moments—three pairwise correlations ρ₁₂, ρ₁₃, ρ₂₃ and three outcome covariances n₁, n₂, n₃—number six, leaving two over-identifying restrictions and hence a genuine test of the uncorrelated-error structure. This is the concrete return to collecting an additional rating, and it is the reason the exercise of Section 5.9 stops where it does.

4. Materials and Methods

4.1. Data

The panel covers 4517 Chinese A-share listed non-financial firms over 2015–2024, comprising 29,434 firm-year observations, with output, capital, labour, intermediate inputs and investment from the China Stock Market and Accounting Research database. The nonparametric measures are available for 3495 firms over 2016–2023. Comparisons that require both families are run on the intersection, which is 20,169 firm-years for 3495 firms for the two level measures; the three Malmquist–Luenberger measures are differences and lose the first year, leaving 16,306 firm-years for 3371 firms. Input and output construction follows the approach standard in the literature on Chinese firm-level productivity [22].

4.2. The Eleven Measures

Five parametric measures were already available in the panel; the five nonparametric measures were produced for this paper by solving programs (3) and (4) of Section 2.2 for every firm-year, under variable returns to scale against a common national frontier. The Olley–Pakes measure was estimated for this paper, since no implementation existed. Stage one regresses log output on log labour and a third-order polynomial in log capital and log investment with year effects, identifying the labour elasticity and the composite φ = β₀ + β_kk + ω. Stage two recovers β_k by minimising the sum of squared innovations under a third-order Markov law of motion for ω. Estimation is performed by two-digit industry for industries with at least 200 observations, with smaller industries pooled. The specification is value-added rather than gross-output, matching the five measures already in the panel; the survival correction of the original paper is not implemented. Olley and Pakes [2] also correct for the probability of survival. That correction needs an exit equation. Listed firms rarely leave the panel, and a delisting in this market mixes poor performance with reorganisation, merger and exchange transfer, so the panel does not contain a clean performance-exit indicator. The correction is omitted for that reason. It would matter if exit were both common and selected on productivity. The first of those conditions does not hold here, and we do not claim that the estimate coincides with a full Olley–Pakes implementation.

4.3. Comparison Design

We report descriptive moments, within- and cross-family correlations in both Pearson and Spearman form, a between/within variance decomposition, quartile reclassification rates relative to the baseline measure and a downstream regression in which each measure in turn is the dependent variable. The downstream specification is identical across measures—firm and year fixed effects, a fixed control vector, standard errors clustered by firm—and the dependent variable is standardised so that coefficients are expressed in standard deviations of the measure and are therefore comparable across measures on different scales.

5. Results

5.1. Levels and Dispersion

Table 1 reports the moments. Mean log productivity ranges from 4.90 to 11.29 across the parametric measures, a spread of more than six log points, and standard deviations differ by a factor of two. Any statement about the level of productivity or about how far a firm sits from the mean is a statement about the estimator as much as about the firm.

Table 1. Descriptive statistics for the eleven productivity measures.

Measure	Family	N	Mean	SD	Min	Max
LP (baseline)	Parametric	29,434	6.868	0.846	3.974	12.651
LP (second implementation)	Parametric	29,434	8.706	1.044	5.740	14.134
Olley–Pakes	Parametric	29,434	4.905	1.295	0.524	13.581
OLS	Parametric	29,434	10.637	1.231	7.404	15.179
Fixed effects	Parametric	29,434	11.290	1.308	7.972	15.596
System GMM	Parametric	29,434	5.849	0.791	3.243	12.191
SBM efficiency score	Nonparametric	20,169	0.078	0.150	0.002	1.000
SBM efficiency level	Nonparametric	20,169	0.927	0.099	0.652	1.414
Malmquist–Luenberger index	Nonparametric	16,306	0.978	0.085	0.670	1.469
ML: efficiency change	Nonparametric	16,306	1.006	0.117	0.751	1.333
ML: technical change	Nonparametric	16,306	0.976	0.039	0.724	1.269

5.2. Rank Agreement Within the Parametric Family

Table 2 shows that the parametric measures largely agree on ordering: Spearman correlations run from 0.83 to 0.999. The agreement is not uniform. OLS and fixed effects are nearly indistinguishable (0.999), which is itself informative—the within transformation is doing little work here—while system GMM and fixed effects agree least (0.83). The Olley–Pakes measure is the least similar to the others, consistent with its different proxy and its restriction to firm-years with positive investment. These correlations are within the parametric family. A low correlation involving Olley–Pakes is a difference between estimators and between the positive-investment observations that proxies uses, not a difference between revenue productivity and an emissions-adjusted distance.

Table 2. Correlations among parametric measures (Pearson below the diagonal, Spearman above).

	LP (Baseline)	LP (Second Implementation)	Olley–Pakes	OLS	Fixed Effects	System GMM
LP (baseline)	1.000	0.945	0.515	0.916	0.899	0.977
LP (second implementation)	0.954	1.000	0.462	0.981	0.973	0.923
Olley–Pakes	0.532	0.478	1.000	0.374	0.353	0.585
OLS	0.923	0.982	0.387	1.000	0.999	0.855
Fixed effects	0.906	0.975	0.365	0.999	1.000	0.833
System GMM	0.980	0.929	0.601	0.861	0.839	1.000

High rank correlation is nonetheless compatible with substantial reclassification. Table 3 reports the share of firm-years that change productivity quartile when the baseline measure is replaced. For the five measures supplied with the panel, the share is between 15.9% and 33.2%. Olley–Pakes, estimated for this paper, moves 53.5%. An earlier draft quoted 16–33% for the supplied measures and omitted that row.

Table 3. Quartile reclassification relative to the Levinsohn–Petrin baseline.

Measure	Share Changing Quartile	Top-Quartile Agreement
LP (second implementation)	25.4%	85.6%
Olley–Pakes	53.5%	57.0%
OLS	30.6%	81.9%
Fixed effects	33.2%	80.0%
System GMM	15.9%	91.6%

5.3. Estimator Labels and the Omitted Intermediate Input

The five measures supplied with the panel carry estimator names, and it is natural to read those names as identifying the technology each assumes. They do not. Recovering the implied elasticities by solving y − TFP = a + β_ll + β_kk within each industry reproduces each measure closely (median R² 0.90–0.99), and the recovered elasticities differ substantially across measures that share a family label. The baseline measure implies a labour elasticity near 0.53 and a capital elasticity near 0.13; the second Levinsohn–Petrin measure implies 0.17 and 0.22. These are not minor implementation differences: they are different production technologies, with implied returns to scale differing by a factor of three across the set. Table 4 reports the recovered values.

Table 4. Factor elasticities implied by each supplied measure (within-industry solve; median and range across industries).

Measure	Median βl	βl Range	Median βk	βk Range	Implied RTS	Median R2
LP (baseline)	0.530	[0.483, 0.627]	0.134	[0.112, 0.164]	0.663	0.994
LP (second implementation)	0.162	[0.142, 0.300]	0.224	[0.190, 0.258]	0.386	0.986
OLS	0.157	[0.146, 0.296]	0.057	[0.045, 0.108]	0.215	0.956
Fixed effects	0.109	[0.102, 0.252]	0.033	[0.025, 0.088]	0.141	0.900
System GMM	0.463	[0.417, 0.569]	0.270	[0.229, 0.288]	0.733	0.995

This has a practical consequence for replication. A reader told only that a study uses “Levinsohn–Petrin TFP” cannot reconstruct the measure, because that label is consistent with the two quite different technologies in the first two rows of Table 4. In our own case, the panel was obtained with the measures pre-computed and without variable labels or generating code, so we can characterise what each measure implies but cannot certify which published estimator produced it. We report the implied elasticities for this reason, and we would encourage the practice generally.

A second feature of the supplied measures emerged from the same exercise and is more consequential than the labelling problem. All five are constructed from gross output, yet none carries an intermediate-input term: the recovered coefficient on log materials is between 0.007 and 0.015 in every case. Intermediate inputs are 67 per cent of output in this panel, so omitting them leaves the largest single input inside the residual. The consequence is visible directly: the correlation between each supplied measure and log materials runs from 0.80 to 0.97. A quantity that correlates at 0.97 with materials usage is, to a first approximation, measuring how much a firm buys rather than how efficiently it converts inputs into output.

Measures of exactly this construction are widely used in the applied literature on Chinese listed firms, which is why the correlation is reported on its own. Li and Yang [23] ask whether ESG-rating disagreement lowers total factor productivity for Chinese A-share firms, and they estimate that relation with Levinsohn–Petrin, Olley–Pakes and GMM. The question in this paper is different: whether changing the productivity measure changes the sign and significance of a downstream coefficient. The omission also compounds the between-firm dominance documented in the next subsection, since materials usage scales with firm size and is therefore largely a cross-sectional attribute. For comparison, the Olley–Pakes measure we estimated ourselves—which also omits a materials term, but whose first stage conditions on a polynomial in capital and investment—correlates with log materials at 0.33 rather than between 0.80 and 0.97.

5.4. Variance Decomposition

Table 5 decomposes the variance of each parametric measure into between- and within-firm components by the law of total variance. The between share is the variance of the firm means and the within share is the variance of the deviations from those means, and the two sum to one. An earlier table reported a between share that did not add to the within share: the variance of unweighted firm means is not the between component once the panel is unbalanced, and for Olley–Pakes, that figure reached 99.4% beside an 8.1% within share. The within shares are unchanged. The corrected between shares run from 86.2% (system GMM) to 91.9% (Olley–Pakes). The share is high enough to bear on how much a fixed-effects design can be asked to do; Gibbons, Suárez Serrato and Urbancic [24] make the related point that absorbing fixed effects can remove most of the variation an applied question depends on. This is a property of these measures in this population rather than a finding that every estimator must divide variance in the same way, and it bounds what a within-firm design can recover from the measure in hand.

Table 5. Between- and within-firm variance decomposition.

Measure	Total Variance	Between	Within
LP (baseline)	0.716	87.4%	12.6%
LP (second implementation)	1.090	90.1%	9.9%
Olley–Pakes	1.677	91.9%	8.1%
OLS	1.516	91.3%	8.7%
Fixed effects	1.712	91.7%	8.3%
System GMM	0.626	86.2%	13.8%

5.5. Agreement Across Families

Table 6 reports rank correlations between the parametric and nonparametric measures. They are small throughout and in one case slightly negative. Fixed-effects TFP and the SBM efficiency score have a rank correlation of −0.021: knowing a firm’s position in one distribution says essentially nothing about its position in the other. The two families are not noisy measurements of a common latent quantity. The two families do not measure one construct. The nonparametric columns incorporate sulphur dioxide and chemical oxygen demand; the parametric rows are revenue residuals and do not. A low rank correlation is therefore not, by itself, evidence that one family is a less reliable estimator of the other family’s object. As a benchmark that holds the estimator fixed and removes the environmental component, we re-solve the slacks-based program on the same 20,169 firm-years, the same labour and capital inputs and the same revenue output, under variable returns and a contemporaneous frontier, but with no undesirable outputs. Table 7 reports the comparison. That conventional score has a rank correlation of 0.70 with the baseline Levinsohn–Petrin measure, against 0.23 for the emissions-adjusted score (and 0.69 with the emissions-adjusted score itself). In the firm-and-year fixed-effects specification used for every measure below, its ESG coefficient is 0.013 (standard error 0.006), positive and significant at 5 percent, rather than the negative and insignificant coefficient on the emissions-adjusted score. Part of the cross-family disagreement is due to the undesirable outputs, not the choice of a frontier estimator as such.

Table 6. Rank correlations (Spearman) between parametric and nonparametric measures.

	SBM Efficiency Score	SBM Efficiency Level	Malmquist–Luenberger Index	ML: Efficiency Change	ML: Technical Change
LP (baseline)	0.233	−0.124	0.014	0.004	0.020
LP (second implementation)	0.078	−0.129	0.011	0.005	0.012
Olley–Pakes	0.274	−0.050	0.016	0.005	0.020
OLS	0.004	−0.138	0.011	0.005	0.010
Fixed effects	−0.021	−0.138	0.010	0.005	0.008
System GMM	0.293	−0.109	0.014	0.003	0.021

Table 7. Conventional SBM without undesirable outputs.

	Conventional SBM	Emissions-Adjusted SBM
Firm-years	20,169	20,169
Firms	3495	3495
Mean	0.032	0.078
Standard deviation	0.077	0.150
Spearman with LP (baseline)	0.699	0.233
Spearman with the emissions-adjusted SBM	0.690	—
ESG coefficient	0.013 **	−0.0081
Standard error	(0.006)	(0.0082)

Notes: Both columns are non-oriented slacks-based measures under variable returns to scale and a contemporaneous frontier, estimated year by year. Inputs are labour and capital; the desirable output is revenue. The conventional score omits sulphur dioxide and chemical oxygen demand; the emissions-adjusted score is the SBM efficiency score in Table 1 and Table 6. Rank correlations are Spearman correlations on the same 20,169 firm-years. The ESG rows use that same firm-and-year specification: firm and year fixed effects, the same controls, firm-clustered standard errors and a standardised dependent variable. The emissions-adjusted ESG coefficient is taken from the SBM efficiency score column of the regression table below. ** p < 0.05.

5.6. The Distance Between Measures

The correlations of Table 2 and Table 6 answer one question—whether two measures move together—and are silent on another: how far apart the distributions they induce actually are. Two measures can be almost perfectly rank-correlated and still assign every firm quite different numbers. The natural metric for the second question is the 1-Wasserstein distance W₁(F, G) = ∫|F⁻¹(u) − G⁻¹(u)| du, the average distance between the two quantile functions, which metrises the space of distributions and is the workhorse of optimal transport [25]; its uses in econometrics run from matching models to vector quantile regression [26,27]. For distributions on the line it is computable directly from sorted samples, so no transport problem need be solved.

Table 8 reports the family averages of the pairwise distances, in two versions. On the raw scales W₁, registers location, scale and shape together: the parametric measures sit an average of 3.27 log points apart, and the two families an average of 7.34—no pair from opposite families is closer than 3.93. After each measure is standardised, so that only shape remains, the pattern inverts. The parametric family collapses to an average distance of 0.06: six estimators that disagree by log points in level are nearly indistinguishable as shapes. The nonparametric measures do not collapse (average 0.33), and the SBM score in particular remains far from everything else.

Table 8. Average 1-Wasserstein distances within and across families.

	Within Parametric	Within Nonparametric	Across Families
Raw scales (location, scale and shape)	3.272	0.391	7.343
Standardised (shape alone)	0.062	0.328	0.225

Notes: Each cell averages the pairwise W₁ distances within the stated block over the eleven measures in Table 1, each computed on that measure’s available sample. In the standardised version, every measure is centred and scaled to unit variance before the distance is taken, so only differences in distributional shape remain. The maximal within-parametric distance is 0.156 after standardisation, against 6.501 before.

The inversion is not an accident; it is Proposition 1 read at the level of distributions. Part (i) says that two parametric measures differ by Δβ_l l + Δβ_k k, a linear function of the inputs, and adding a linear combination of regressors to a variable shifts and stretches its distribution while leaving its shape close to intact. That the parametric family disagrees almost entirely in location and scale, and almost not at all in shape, is therefore the distributional signature of the proposition—and the fact that the nonparametric family shows no such collapse says again, in metric form, that it is not related to the parametric family by any such linear map.

5.7. Consequences for Applied Inference

The comparison that matters for practice is Table 9. Each measure in turn is regressed on a firm’s ESG rating with firm and year fixed effects and a fixed control vector, on the widest sample each measure permits—20,169 firm-years for 3495 firms, or 16,306 for 3371 firms for the three differenced measures—with the dependent variable standardised. All six parametric measures produce a positive coefficient significant at the 1% level. All five nonparametric measures produce a coefficient that is statistically indistinguishable from zero and negative in sign. The control set, the fixed effects and the clustering are the same in every column. The samples are not: the level measures use 20,169 firm-years and the three differenced measures use 16,306. On the 16,306 firm-years for which all eleven measures are observed, the six parametric coefficients remain between 0.014 and 0.025 and the five nonparametric coefficients remain between −0.009 and −0.002, so the contrast is not an artefact of sample composition. It is also not a test that the coefficients differ from each other. A coefficient that is significant in one column and insignificant in another need not be statistically distinguishable from its neighbour. Part of the contrast is a difference of construct: the nonparametric measures penalise undesirable outputs and the parametric measures do not.

Table 9. The same regression under eleven productivity measures.

Measure	Family	ESG Coefficient (SD Units)	SE	p
LP (baseline)	Parametric	0.0288 ***	(0.0042)	<0.01
LP (second implementation)	Parametric	0.0313 ***	(0.0038)	<0.01
Olley–Pakes	Parametric	0.0150 ***	(0.0039)	<0.01
OLS	Parametric	0.0304 ***	(0.0035)	<0.01
Fixed effects	Parametric	0.0302 ***	(0.0034)	<0.01
System GMM	Parametric	0.0286 ***	(0.0044)	<0.01
SBM efficiency score	Nonparametric	−0.0081	(0.0082)	n.s.
SBM efficiency level	Nonparametric	−0.0082	(0.0061)	n.s.
Malmquist–Luenberger index	Nonparametric	−0.0074	(0.0110)	n.s.
ML: efficiency change	Nonparametric	−0.0019	(0.0106)	n.s.
ML: technical change	Nonparametric	−0.0080	(0.0095)	n.s.

Firm and year fixed effects; controls: leverage, ROA, cash flow, sales growth, loss indicator and listing age. Standard errors clustered by firm. Dependent variable standardised. *** p < 0.01. n.s., not significant.

5.8. The Closed Form for Parametric Disagreement

Proposition 1 says the parametric block of Table 9 is not a scatter of independent estimates but a set of points determined by the technologies the measures assume. It can be checked directly. Projecting log labour and log capital onto the ESG rating under the baseline specification gives γ_l = 0.043 and γ_k = 0.047. Substituting these and the implied elasticities from Table 4 into Equation (8) yields, for each of the ten pairs of parametric measures, a predicted gap between their ESG coefficients. Table 10 sets the predictions beside the gaps actually realised.

Table 10. Coefficient gaps among parametric measures: closed form against realised.

Pair	Predicted by (8)	Realised	Difference
LP (baseline) − LP (second)	−0.01139	−0.01123	0.00016
LP (baseline) − OLS	−0.01943	−0.01940	0.00004
LP (baseline) − Fixed effects	−0.02264	−0.02261	0.00003
LP (baseline) − System GMM	0.00355	0.00366	0.00011
LP (second) − OLS	−0.00805	−0.00817	−0.00012
LP (second) − Fixed effects	−0.01126	−0.01138	−0.00012
LP (second) − System GMM	0.01494	0.01489	−0.00004
OLS − Fixed effects	−0.00321	−0.00321	−0.00000
OLS − System GMM	0.02299	0.02306	0.00007
Fixed effects − System GMM	0.02620	0.02627	0.00008

Notes: γ_l and γ_k are the coefficients on the ESG rating in projections of log labour and log capital under the baseline specification. Implied elasticities are those of Table 4. N = 29,434.

The agreement is essentially exact. Predicted and realised gaps correlate at 1.000, and the mean absolute discrepancy is 0.00008—half of one per cent of the standard deviation of the gaps themselves. The disagreement among parametric measures in an applied regression is therefore not residual noise to be averaged over or bootstrapped away. It is an arithmetic consequence of the factor shares each measure imposes, and it would persist unchanged in a sample of any size.

5.9. How Much of the ESG Rating Is Signal

The panel carries a second rating, from SynTao Green Finance, for 15,498 of the firm-years used here, which makes Propositions 2 to 4 operational. That the agencies disagree is by now well documented: Berg, Kölbel and Rigobon [16] report pairwise correlations between 0.38 and 0.71 among six major providers and attribute the divergence to scope, measurement and weighting, and Christensen, Serafeim and Sikochi [17] find that disclosure widens rather than narrows it. The two ratings used here correlate at 0.460 in levels but at only 0.315 within firms—the reduction Proposition 2 anticipates, since a rating’s signal is largely a cross-sectional attribute while its error is not. Applying (12) recovers the two reliabilities separately. Table 11 reports them, with confidence intervals from 400 firm-level bootstrap replications.

Table 11. Reliability of each rating agency, recovered from Equation (12).

Outcome Measure	λ21 Huazheng	95% CI	λ22 SynTao	95% CI	Disattenuated β
LP (baseline)	0.154	[−0.032, 0.343]	0.821	[−3.712, 7.786]	0.0087
LP (second)	0.222	[0.123, 0.365]	0.569	[0.350, 1.052]	0.0156
OLS	0.260	[0.167, 0.387]	0.486	[0.318, 0.723]	0.0216
Fixed effects	0.269	[0.175, 0.380]	0.470	[0.331, 0.723]	0.0238
System GMM	0.089	[−0.203, 0.391]	1.425	[−6.228, 10.416]	0.0053

Notes: λ²_j is the within-firm reliability of agency j’s rating after firm and year effects and the control vector are partialled out. Intervals are percentile intervals from 400 bootstrap replications resampling firms. N = 15,498 firm-years across 4224 firms.

The two agencies are not equally informative. Across the three specifications in which the ratio is estimated precisely, the Huazheng rating carries a within-firm reliability of 0.22 to 0.27 while the SynTao rating carries 0.47 to 0.57—roughly twice the signal. An analysis that assumed the agencies were equally reliable, as a symmetric two-indicator model does, would understate one and overstate the other by about that factor. The two remaining rows are reported for completeness but should not be read: where the outcome covaries only weakly with the second rating, the reliability is a ratio of two small numbers and its interval spans implausible values. Rows whose confidence intervals leave the unit interval, or whose point estimate exceeds one, are not reliabilities. The system-GMM row is the clearest case: the SynTao figure is 1.425 with an interval from −6.2 to 10.4. That is a ratio of small moments, not a finding about the agency.

What the design cannot do is check its own premise. By Proposition 4(ii) the system is exactly identified, so the assumption that the two agencies’ errors are uncorrelated—doubtful on its face, since both read the same disclosures—leaves no observable trace. We therefore report the disattenuated coefficients as what the design implies under its assumption, not as corrected estimates, and note that a third rating would be required to do better. The assumption is restrictive for a further, practical reason. Both agencies read overlapping disclosures and public filings, so their errors can share a component even when neither rating is the other’s input. Corollary 3 gives the direction of the resulting bias. It does not replace the missing test.

5.10. An Estimator That Does Not Survive the Exercise: Ackerberg–Caves–Frazer

We attempted to add the Ackerberg, Caves and Frazer [4] estimator as a seventh parametric measure. It is the natural modern addition, since it is designed to repair the functional-dependence problem in the first stage of the proxy-variable estimators. We report the attempt because it failed, and because the way it failed is relevant to the paper’s subject.

The implementation follows the standard design: a third-order polynomial first stage in labour, capital and materials from which only the composite is retained, and a second stage in which the elasticities are recovered jointly from the moment conditions that the productivity innovation be orthogonal to current capital and lagged labour. Estimated without restrictions, the criterion is minimised at values that cannot be interpreted as a production technology; one industry returned a labour elasticity of −31.8. Restricting the search to the economically admissible region moves the optimum to the boundary of that region in ten of the seventeen industry groups, with implied returns to scale as low as 0.03. The same caution applies to Table 4, which is not a Monte Carlo experiment. Implied returns to scale of 0.141 for the fixed-effects residual and 0.215 for the OLS residual are not estimates of technology we would defend. They record what those supplied series encode. Together with the ACF boundary results, they are a reason to treat an estimator label as a claim that has to be checked, not as evidence that estimators of one object merely disagree.

A flatness diagnostic shows that this is not the familiar weak-identification story: only 0.2–3.4 per cent of the admissible parameter grid lies within one per cent of the minimised criterion, so the criterion has a well-defined minimum. The minimum simply lies outside the economically admissible region, which indicates that the moment conditions are not satisfied at any plausible parameter vector in this panel rather than that the data are uninformative about where the optimum is. We therefore do not report ACF as a measure. Reporting it would have added a column of numbers we do not believe to a paper whose argument is that such numbers are consequential, and the honest conclusion is that the practical estimator menu for this kind of panel is narrower than the methodological literature suggests.

6. A Monte Carlo Experiment

Section 5.6 and Section 5.7 show that measurement choice moves the applied estimand and that Proposition 1 accounts for the movement. Neither exercise can say which measure is closer to the truth, because on real data the technology is unobserved. In simulation it is not.

6.1. Design

Output is Cobb–Douglas in labour and capital with elasticities β_l = 0.6 and β_k = 0.4 and a persistent productivity term:

ω_it = μ_i + a_it, a_it = ρ a_i,_t−1 + θ s_it + ξ_it, y_it = β_l l_it + β_k k_it + ω_it + ε_it,

(13)

with ρ = 0.7 and θ = 0.05. Labour is chosen with the current shock known, which is what makes least squares inconsistent, but an idiosyncratic wage shock keeps it from being a sufficient statistic for productivity. Capital is predetermined: investment responds to the current shock, and an installation shock realised after the investment decision gives capital variation of its own without disturbing the invertibility the proxy estimators require. Materials and investment are near-deterministic functions of (ω, k), as the scalar-unobservable assumption demands. Panels have 800 firms over ten periods after a six-period burn-in, and every figure below averages 200 replications. Each panel comprises 200 independent draws. Five estimators are applied to every draw, which is why the proposition check below refers to 1000 estimator-replications. Those are not 1000 Monte Carlo replications.

The regressor s raises productivity by θ, so the object of interest is well defined. Each estimator delivers m^{^} = y − β^{^}_l l − β^{^}_k k, which is regressed on s with firm and year effects. The benchmark is the same regression run on the measure built with the true elasticities, y − β_l l − β_k k: it carries the same output shock as every candidate, so the comparison isolates the effect of getting the technology wrong rather than the noise both share.

Two productivity processes are simulated. In panel A, μ_i = 0 and productivity is first-order Markov, which is exactly the assumption the proxy-variable estimators maintain. In panel B, μ_i is a permanent firm component with a standard deviation of 0.8, so the assumption fails. Panel B is the empirically relevant case: Section 5.4 finds about 86 to 92 per cent of the variance of every measure to lie between firms. The permanent component is not only switched on at a single large value. Section 6.2 also reports the capital elasticity at standard deviations of 0, 0.2, 0.4, 0.6 and 0.8.

6.2. Monte Carlo Results

Table 12 reports the average recovered elasticities, the downstream coefficient, its bias against the benchmark, and the bias Proposition 1 predicts. Three things stand out.

Table 12. Monte Carlo: recovered elasticities and downstream bias, 200 replications.

Estimator	βl	βk	θ^	Bias vs. Benchmark	Predicted by (8)
Panel A. Productivity is first-order Markov
OLS	0.7286	0.4392	0.0393	−0.0023	−0.0023
Fixed effects	0.6876	0.3511	0.0396	−0.0019	−0.0019
Levinsohn–Petrin	0.6025	0.4065	0.0415	−0.0000	−0.0000
Olley–Pakes	0.6025	0.4050	0.0415	−0.0000	−0.0000
Differenced GMM	1.1354	−0.2500	0.0279	−0.0137	−0.0137
Benchmark (true elasticities)	0.6000	0.4000	0.0415	—	—
Panel B. Productivity has a permanent firm component
OLS	0.9587	0.9348	0.0365	−0.0047	−0.0047
Fixed effects	0.6870	0.3315	0.0392	−0.0020	−0.0020
Levinsohn–Petrin	0.6026	1.0368	0.0439	0.0027	0.0027
Olley–Pakes	0.6026	1.0363	0.0439	0.0027	0.0027
Differenced GMM	0.9519	0.0369	0.0327	−0.0085	−0.0085
Benchmark (true elasticities)	0.6000	0.4000	0.0412	—	—

Notes: A total of 800 firms over ten periods, 200 replications and true elasticities β_l = 0.600 and β_k = 0.400. θ^{^} is the coefficient on s in a regression of each measure with firm and year effects; the benchmark is the same regression on the measure built with the true elasticities. γ_l = 0.0192 and γ_k = −0.0049 in panel A, 0.0197 and −0.0044 in panel B. Predicted and realised bias correlate at 1.00000 in both panels, with mean absolute discrepancies of 5.9 × 10⁻¹⁷ and 6.0 × 10⁻¹⁷.

First, Proposition 1 is exact. Across 1000 estimator-replications in each panel, predicted and realised bias agree to machine precision—the mean absolute discrepancy is of order 10⁻¹⁷. This is not an approximation that happens to work well; part (ii) of the proposition is an identity, and nothing in it is estimated.

Second, when the Markov assumption holds, the proxy estimators do what they are designed to do. Levinsohn–Petrin recovers (0.603, 0.407) and Olley–Pakes (0.603, 0.405) against a truth of (0.600, 0.400), and their downstream coefficients are unbiased to four decimal places. Least squares and fixed effects overstate the labour elasticity, and the differenced GMM estimator—weakly identified when the series are persistent, the difficulty the system estimator was introduced to remove—understates the downstream coefficient by a third.

Third, and least comfortably, the ranking reverses once productivity carries a permanent component. The proxy estimators still recover the labour elasticity, but their capital elasticity rises to 1.04, two and a half times the truth, because the firm effect enters what the second stage treats as the productivity innovation and is correlated with capital. The fixed-effects estimator, which this literature regards as inconsistent, is then the closest of the five on capital. No estimator is uniformly best, and which is least bad turns on whether productivity carries a permanent firm component—a feature of the environment that applied data cannot settle, since a permanent component and a highly persistent Markov process are observationally similar over a ten-year panel. Along that path, the proxy estimators’ capital elasticity, whose truth is 0.40, is as follows: at 0.0: LP 0.41, OP 0.40, FE 0.35; at 0.2: LP 0.65, OP 0.65, FE 0.24; at 0.4: LP 0.88, OP 0.88, FE 0.28; at 0.6: LP 1.00, OP 1.00, FE 0.31; and at 0.8: LP 1.04, OP 1.04, FE 0.33. The overstatement grows with the permanent component rather than appearing only at 0.8. Each cell averages the same 200 replications, re-seeded at each value.

That is what the simulation adds. The measures disagree; Proposition 1 says exactly how much; and the question of which to prefer rests on an assumption that is maintained rather than tested.

7. Discussion

Three readings of Table 9 are available, and they have different implications. The first is that the parametric result is right and the nonparametric measures are too noisy to detect it. This is possible but does not fit the standard errors, which are of a similar order across families. The second is that the nonparametric result is right and the parametric association reflects revenue rather than physical efficiency—higher-rated firms may command price premia that revenue-based TFP cannot separate from technical improvement. The third, which we regard as the most defensible, is that the two families answer different questions: the parametric measures ask how much output a firm obtains from its measured inputs, and the nonparametric measures used here ask how close it operates to a frontier that penalises undesirable output. A firm can improve on one margin while not improving, or while deteriorating, on the other.

If the third reading is correct, the practical implication is not that one family should be preferred but that results obtained under one should not be cited as evidence for the other. This is currently common. Studies reporting that a firm characteristic “raises productivity” using revenue-based parametric TFP and studies reporting the same using green productivity indices are routinely cited together, and the evidence here indicates that they are not measuring the same thing closely enough for that to be sound.

The variance decomposition adds a constraint that applies to both families. With about 86–92% of productivity variation lying between firms, within-firm designs are identified from a small fraction of the total dispersion. This is a plausible reason why within-firm estimates in this literature are often small and imprecisely determined even in large samples, and it suggests that the leverage of additional observations is limited relative to the leverage of better measurement.

8. Conclusions

Measurement choice in firm-level productivity analysis is consequential in a way that current practice does not reflect. Within the parametric family, estimators agree on ordering while disagreeing on levels sufficiently to reclassify a third of firm-years. Across families, agreement is close to zero. Under one specification, the parametric measures produce a significant positive association, and the nonparametric measures do not. That contrast survives a common sample, but it mixes estimator choice with a difference in construct, and it is not a formal test that the coefficients differ. Robustness checks drawn from a single family, which is the prevailing convention, do not test the assumption that matters most.

Three implications follow for applied work. Report the production-function specification and the estimator explicitly, since the same label covers implementations with materially different factor shares. Draw robustness checks from across families rather than within one. And state which construct the conclusion refers to—revenue productivity, physical efficiency or environmentally adjusted efficiency—because the evidence here indicates these are separable in practice and not merely in principle.