Investment Behavior, Observable Expectations, and Internal Funds Jason G. Cummins ? Assistant Professor New York University 269 Mercer Street New York, NY 10003 [email protected] nyu. edu Kevin A. Hassett Resident Scholar American Enterprise Institute 1150 17th Street NW Washington, DC 20036 [email protected] org Stephen D. Oliner Asst. Dir. of Research Federal Reserve Board Mail Stop 93 Washington, DC 20551 [email protected] gov First Draft: September 8, 1997 Second Draft: July 6, 1998 Third Draft: March 31, 1999
Abstract We use earnings forecasts from securities analysts to construct more accurate measures of the fundamentals that a? ect the expected returns to investment. We ? nd that investment responds signi? cantly — in both economic and statistical terms — to our new measures of fundamentals. Our estimates imply that the elasticity of the investmentcapital ratio with respect to a change in fundamentals is generally greater than unity. In addition, we ? d that internal funds are uncorrelated with investment spending, even for selected subsamples of ? rms — those paying no dividends and those without bond ratings — that have been found to be “liquidity constrained” in previous studies. Our results cast doubt on the evidence for liquidity constraints from the many studies that have used Tobin’s Q to control for the expected returns to investment. JEL Classi? cation: D92, E22. Keywords: Investment; Tobin’s Q; Cash Flow; Liquidity Constraints.
We thank Steve Bond, Ricardo Caballero, Mark Gertler, Simon Gilchrist, John Hand, Glenn Hubbard, Steve Kaplan, Owen Lamont, Plutarchos Sakellaris and seminar participants at Brandeis University, UC Berkeley, the Econometric Society Winter Meetings, the Federal Reserve Board, University College London, the University of Maryland, the NBER Economic Fluctuations and Monetary Economics Program Meetings, Northwestern University, New York University, Tilburg University, and Yale University for helpful comments and suggestions. Cummins gratefully acknowledges ? nancial support from the C. V. Starr Center for Applied Economics.
The views expressed in this paper are those of the authors, and do not re? ect those of the Board of Governors of the Federal Reserve System or its sta?. The data on earnings expectations are provided by I/B/E/S International Inc. ? Presenting/Corresponding author. 1 Introduction Until recently, the consensus among researchers was that neoclassical fundamentals fail to explain the observed movements in business investment (see, e. g. , Chirinko 1993). For example, in a well-known study, Summers (1981) found that a one percent increase in the shadow value of capital increases investment by a paltry 0. 2 percent. Furthermore, models derived from neoclassical fundamentals have fared poorly in horseraces against ad hoc accelerator models of investment (see, e. g. , Bernanke, Bohn, and Reiss 1988). This result could re? ect the consequences of asymmetric information in ? nancial markets: Lenders become more favorably inclined to make loans when a ? rm’s net worth improves, leading to an expansion of business investment. In an important study, Fazzari et al. (1988) used ? rm-level panel data to try to isolate ? rms for which investment may be constrained by internal funds.
They found that the ? rms most likely to face liquidity constraints tend to have the highest sensitivity of investment to cash ? ow. Subsequent empirical research has generally supported this ? nding. 1 Although this literature suggests that neoclassical models of investment perform poorly because many companies face ? nancial constraints, such a conclusion may be premature. A parallel literature, which attempts to control more fully for measurement error and allows non-convexities in marginal adjustment costs, has shown that neoclassical fundamentals are important determinants of investment.
For example, Cummins and Hassett (1992) and Cummins, Hassett, and Hubbard (1994) used ? rm-level panel data to construct tax instruments for changes in tax-adjusted Tobin’s Q and the cost of capital, and found that both variables have sizable e? ects on investment following major U. S. tax reforms. Cummins, Hassett, and Hubbard (1995) found even larger responses following tax reforms in a sample of ? rms in 12 industrialized countries. Other studies showed that investment responds signi? cantly to average Q at relatively low values of Q but little, if at all, at high values (see, e. . , Abel and Eberly 1996; Barnett and Sakellaris 1998). When this nonlinearity is ignored these studies found that the coe? cient estimate on average Q implies incorrectly that fundamentals have a negligible e? ect in the sample as a whole. Consistent with this ? rm-level research, Caballero, 1 For a recent survey of the literature on capital-market imperfections and investment see Hubbard (1998). 1 Engel, and Haltiwanger (1995) found that neoclassical fundamentals have large e? ects on investment in plant-level data. Given the results in this parallel literature, those who believe that ? nancial factors drive investment face something of a puzzle. How can ? ndings that support the neoclassical model be reconciled with the results of many studies that report a strong positive e? ect of internal funds on investment? We address this puzzle by building on the observation that neoclassical models perform well only if one has good measures of the fundamentals that drive investment. Although this requirement has long been recognized, it is often paid only lip-service in empirical research on investment.
In particular, many studies have continued to use Tobin’s Q as a measure of fundamentals despite its disappointing track record. We depart from prior work by employing ? rm-speci? c earnings forecasts from securities analysts to control for expected future pro? ts. The forecasts are compiled by I/B/E/S International Inc. , a private data vendor with extensive ties to the analyst community. Our approach side-steps the di? cult problem of selecting a speci? c forecasting model for each ? rm. The professional analysts who track these companies do that for a living, and their expectations are observable.
We use the analysts’ earnings expectations in two ways. First, we include these expectations as instruments in a standard investment model that features Tobin’s Q as the proxy for fundamentals. In this way, we employ a larger and — we hope — more informative instrument set than in previous studies. Second, we construct a new measure of fundamentals from the earnings expectations, which we call “real Q”. With real Q serving as the control for the expected returns to investment, we estimate some models that circumvent the use of Tobin’s Q entirely.
To connect with previous empirical work on investment, we start with the speci? cation often used to examine the role of ? nancing constraints — that is, we regress investment on Tobin’s Q and cash ? ow, where investment and cash ? ow are both scaled by the replacement value of the capital stock. In this framework, the coe? cient on cash ? ow measures its in? uence after controlling for expected future returns, and it should be zero if there are no binding ? nancial constraints. We estimate this linear model 2 For reviews of this more recent literature, see Caballero (1997) and Hassett and Hubbard (1997). with OLS and then with the generalized method of moments (GMM), as the OLS estimates are consistent only under restrictive conditions; our GMM procedure employs a standard instrument set, which contains lags of investment and cash ? ow (both scaled by the replacement value of the capital stock) and Tobin’s Q. The results from these baseline linear regressions are consistent with those in much past work: We ? nd small and sometimes insigni? cant coe? cients on Tobin’s Q, while cash ? ow has a signi? cant e? ect on investment.
However, the econometric properties of this model are poor: The residuals display a high degree of serial correlation, and diagnostic tests reject the hypothesis that the model and the instrument set are properly speci? ed. We then examine the robustness of this baseline model in several ways. Our alternative speci? cations include: (1) OLS estimation with real Q replacing Tobin’s Q as the control for fundamentals and (2) GMM estimation with a variety of instrument sets that replace lags of Tobin’s Q with lags of either sales, analysts’ earnings expectations, or both.
The results obtained from all these alternatives are roughly the same — and in sharp contrast to those from the baseline speci? cation. Notably, the controls for fundamentals now have large and statistically signi? cant e? ects on investment. In this regard, the GMM estimates imply that the elasticity of the investment-capital ratio with respect to either Tobin’s Q or real Q is generally above unity, when evaluated at the sample medians; the elasticity evaluated at the sample means is typically 25 to 50 percent greater. Moreover, we ? nd that the coe? cient on cash ? w becomes uniformly insigni? cant, even for subsamples of ? rms that are often claimed to be liquidity constrained — those that pay no dividends and those without bond ratings. Finally, the econometric properties of the model improve dramatically. In our preferred GMM speci? cations, we no longer reject the model or the validity of the instruments, nor do we ? nd evidence of serial correlation in the residuals (beyond that induced by our ? rst-di? erencing of the data). Our results strongly caution against using Tobin’s Q to estimate investment models.
First, Tobin’s Q is a noisy control for fundamentals; only the portion that is correlated with the ? rm’s past performance or its expected earnings helps to explain investment spending. Second, lags of Tobin’s Q appear to be invalid instruments; merely replacing them in the instrument set greatly improves the economic and statistical properties of 3 the estimates. These problems likely indicate that Tobin’s Q is measured with error and that the error is serially correlated. Another implication of our results is that analysts’ earnings expectations convey valuable information about investment — certainly a lot more than Tobin’s Q.
Armed with just these expectations, we show that one can construct a model of ? rm-level investment with desirable properties and can forecast the time-series movements in aggregate investment with considerable accuracy. Nonetheless, the emphasis we place on analysts’ expectations is more nuanced than in previous versions of this paper. As we document in section 4, most of the results we obtain with analysts’ expectations as instruments also can be generated with an instrument set that includes only lags of sales, cash ? ow, and investment.
This suggests that most of the information about investment in analysts’ forecasts can be spanned with more easily available accounting data. Our work is part of a growing e? ort to reassess previous research on investment and internal funds. In a well-known paper, Kaplan and Zingales (1997) used a simple model to show that the degree of a ? rm’s ? nancing constraint need not vary monotonically with its cash-? ow sensitivity — thus calling into question the basic assumption behind many papers in this literature. To illustrate this point, they scrutinized the sample of low-dividend ? ms for which Fazzari et al. (1988) had found an especially strong correlation between investment and cash ? ow, holding fundamentals constant. Based on their reading of ? nancial reports for these 49 ? rms, Kaplan and Zingales judged that the ? rms with the greatest cash ? ow sensitivity actually were unconstrained. 3 Hayashi (1997) re-examined the results of another prominent paper in this literature, the Hoshi, Kashyap, and Scharfstein (1991) study of Japanese companies, which found that cash ? ow had a much stronger e? ect on investment for independent ? ms than for those with close ties to banks through their membership in a Keiretsu. Hayashi showed that this result is fragile. Using a parallel dataset that likely contains more accurate measures of investment and the capital stock, he found much less di? erence in cash ? ow coe? cients across the two groups than did Hoshi et al. (1991) and no di? erence at all after removing four extreme data points. 3 This assertion generated a lively debate; see the reply in Fazzari et al. (1996). Also see Cleary (1999), who used factor analysis to classify (a di? erent set of) ? rms by degree of ? ancial constraint and obtained results similar to those of Kaplan and Zingales. 4 The studies that bear the closest resemblance to our paper are Erickson and Whited (1998) and Whited (1999). Both studies estimate investment equations using a GMM framework that explicitly allows for measurement error in Tobin’s Q. Erickson and Whited (1998) provide a taxonomy of the possible sources of this error. 4 Moreover, they estimate that the amount of measurement error in Tobin’s Q is substantial: Movements in true marginal q account for as little as 40 percent of the observed variation in ? m-level Tobin’s Q. Although both studies obtain positive cash-? ow coe? cients in baseline OLS regressions, these coe? cients become uniformly insigni? cant in their GMM procedure. We reach the same conclusion, but we use an estimation technique that hews much more closely to the methods typically employed in the investment literature. Our paper — combined with Kaplan and Zingales (1997), Hayashi (1997), Erickson and Whited (1998), and Whited (1999) — casts doubt on the evidence for liquidity constraints from the many studies that have estimated the Q model augmented with measures of liquidity.
In the next section, we present the standard Q model of investment, review how it is estimated, and discuss how analysts’ earnings forecasts can be used to aid in estimation. Section 3 describes the data, while section 4 presents our results. The ? nal section concludes and suggests directions for future research. 2 Basic Investment Model 2. 1 The Model The model we use is a standard one in the investment literature. The ? rm maximizes the expected present discounted value of future pro? ts at time t:5 ? s Et s=t j=t ?j ?(Ks? 1 ) ? C(Is , Ks? 1 , ? s ) ? Is , (1) eading candidates include violations of the stringent assumptions needed for average Q to equal the underlying marginal q that drives investment, and ine? ciencies in the equity market that would cause the ? rm’s assessment of its prospects to di? er from that embedded in Tobin’s Q. 5 The ? rm index i is suppressed except when needed to avoid confusion. 4 Two 5 where Et is the expectations operator conditional on the set of information available at the beginning of period t, ? t? 1 ; ? s = (1 + ? s )? 1 is the time s discount factor; Is is gross investment; Ks? is the replacement value of the capital stock at the beginning of period s; ? (Ks? 1 ) represents the revenue function; and C(Is , Ks? 1 , ? s ) is the adjustment cost function, which includes the productivity shock ? s as an argument. We assume that capital is the only quasi-? xed factor and that variable factors have been maximized out of ?. For convenience in presenting the model, we also assume that the price of investment relative to output is unity and that there are no taxes. In our empirical work we incorporate data on the after-tax price of investment to construct tax-adjusted Tobin’s Q.
The adjustment cost technology and the productivity shock are discussed in detail below. Firms maximize equation (1) by choosing It for all periods t, subject to the usual constraint on their capital stock: Kt = (1 ? ?)Kt? 1 + It , where ? is the rate of economic depreciation. The ? rst-order condition for this constrained maximization is: 1+ ? C(It , Kt? 1 ) = qt . ?It (2) This equation shows that the full cost of acquiring and installing a unit of capital must equal q, the shadow price of capital. The shadow price evolves according to: Et ? t+1 ?? ?C ? ?Kt ? Kt = qt ? (1 ? ?)Et ? t+1 qt+1 . (3)
Solving equation (3) for its stationary solution, we obtain the following expression for marginal q: ? qt = Et s=t (1 ? ?)s? t s ?j+1 j=t ?? ?C . ? ? Ks ? Ks (4) Equation (4) states that marginal q equals the present discounted value of the stream of net revenue generated by the marginal unit of undepreciated capital. 6 Given an explicit form for the adjustment cost function, equation (2) can be manipulated to express the investment-capital ratio in terms of marginal q. The adjustment cost technology we choose is a standard one in the investment literature (adding the ? rm index i): C(Iit , Ki,t? 1 ) = Iit ? ? ? ? it 2 Ki,t? 1 2 Ki,t? 1 . (5) In this function, adjustment costs are convex in net investment. 6 If we substitute ? C(Iit ,Ki,t? 1 ) ? Iit into equation (2) and rearrange terms, we obtain a simple equation linking investment to marginal q: Iit Ki,t? 1 =? + 1 qit ? 1 + ? it . ? (6) We assume that the productivity shock ? it is the sum of three mean-zero components: ? it = ? i + ? t + it , (7) where ? i accounts for unobserved ? rm-speci? c heterogeneity, assumed to be constant over time; ? t captures cyclical factors that have a common e? ect on all ? rms; and the ? nal component, assume it it , s a stochastic disturbance to the ? rm’s production process. We is independently and identically distributed (iid) across ? rms, but can be serially correlated over time for each ? rm. 7 Equation (6) is a standard empirical formulation of the neoclassical investment model under the null of perfect capital markets. 8 Numerous studies have used this equation to test the null against the alternative in which ? nancial factors a? ect investment. The usual procedure is to augment equation (6) with a variable — typically, cash 6 Alternatively, adjustment costs could be modeled as a convex function of gross investment.
The distinction is of little importance in the Q-model since the e? ect of depreciation is captured in the constant term of the regression equation. 7 Alternatively, one can think of it as a measurement error or optimization error that allows the ? rm’s ? rst-order conditions to be satis? ed only in expectation (from the perspective of the econometrician). 8 There are several other ways to obtain empirical representations of the neoclassical investment model. The most common alternative is based on the Euler equation obtained by substituting equation (2) into (3) to eliminate terms in q. ?ow — that contains information about a ? rm’s ? nancial position. However, this approach yields valid tests only if marginal q is accurately measured. The problem is that measures of internal net worth, like cash ? ow, signal not only the ? rm’s ? nancial position, but also may be correlated with its expected investment opportunities. If marginal q is mismeasured, the estimated coe? cient on cash ? ow could be positive and statistically signi? cant even if the null model is correct. This concern is what motivates the empirical work in our paper. 2. 2 Estimation
We use two alternative approaches to proxy for (unobservable) marginal q in equation (6). First, to conform with much prior research, we use Tobin’s average Q, de? ned as the ratio of the market value of the ? rm to the replacement value of its capital stock. Our particular measure contains a variety of tax adjustments and is de? ned by equation (A. 1) in appendix A. Hayashi (1982) provided the theoretical basis for the use of Tobin’s average Q, showing that it equals marginal q when the ? rm has a linear homogeneous net revenue function and operates in perfectly competitive markets.
In addition, the asset prices used to construct Tobin’s Q must provide a noise-free signal about the ? rm’s fundamentals. Obviously, these are strong requirements. By itself, the substantial evidence of excess volatility in stock prices (see, e. g. , Shiller 1989) raises questions about the use of Tobin’s Q. Our second proxy for fundamentals is based on analysts’ earnings expectations. As we discuss in more detail below, the I/B/E/S data contain three variables that can be used to control for fundamentals: One- and two-year-ahead earnings forecasts, and a forecast of long-term earnings growth.
We combine the forecasts into a tightly speci? ed formulation called “real Q”. This speci? cation, like that for Tobin’s Q, relies on Hayashi’s result that links measures of average Q and marginal q in equation (4). 9 9 Caballero and Leahy (1996) argue that average Q, not marginal q, is the correct measure of fundamentals when there are certain types of ? xed costs. While it not possible for us to directly identify ? xed costs in our ? rm-level data, our approach is consistent with their study since we use average Q to approximate marginal q. Our empirical results support their suggestion to interpret the signi? ance of cash ? ow in investment equations not as a signal of the presence of liquidity constraints, but as a variable that helps capture fundamentals. 8 Real Q is constructed in the following way. Let ECFit and ECFi,t+1 denote the ? rm’s expected net income in periods t and t + 1, respectively, with each scaled by the replacement value of the capital stock at the beginning of period t, and let EGRit denote the ? rm’s expected growth rate of net income in the following periods. All these expectations are formed at the beginning of period t. We calculate the implied level of net income for eriods after t + 1 by growing out the average of ECFit and ECFi,t+1 at the rate of EGRit . 10 The resulting sequence of net incomes (which we have scaled by the replacement value of the capital stock at the beginning of period t) de? nes real Qit : Real Qit = ? ECFit + ? 2 (1 ? ?)ECFi,t+1 + ECFit + ECFi,t+1 2 n k=3 ?k (1 ? ?)k? 1 (1 + EGRit )k? 2 . (8) This expression for real Q mimics that for marginal q in equation (4) except that we proxy for the unobserved future marginal products of capital with an approximation for the future average products based on the I/B/E/S earnings forecasts.
We set the constant discount factor, ? , to 0. 91 (re? ecting a 10 percent nominal interest rate, ? = 0. 10), and the depreciation rate to the sample mean of the data, about 0. 15. Our empirical results were similar when we used ? rm- or industry-speci? c data on discount factors (based on S&P bond ratings) and depreciation rates. In principle, the value of n — the horizon for calculating real Q — should be in? nity. However, the analysts estimate EGR over a horizon of no more than ? ve years, so we lack information for the later years. We experimented with values of n ranging from ? e to ten years and found that our qualitative results were not sensitive to this choice. Thus, somewhat arbitrarily, we set n equal to ten years in equation (8). 11 We constructed two other variants of real Q for our empirical analysis. The ? rst is what we call “terminal value real Q”, which augments real Q with an estimate of 10 We grow out the average of the one- and two-year-ahead forecasts rather than the two-year-ahead forecast because I/B/E/S de? nes EGR as the expected trend growth of the company’s earnings, not the growth rate from the two-year-ahead forecast of earnings. 1 The expression for real Q is also less than ideal for one additional reason. To approximate the average product of capital, the projected net income for a given future period should be scaled by the beginningof-period capital stock for that period. However, future values of the ? rm’s capital stock are unknown forcing us to use the beginning-of-period t value instead. 9 earnings beyond year ten: Terminal Value Real Qit = Real Qit + ECFit + ECFi,t+1 1 ? n+1 (1 ? ?)n (1 + EGRit )n? 1 ? 2 (9) . The terminal value correction is, in e? ect, a perpetuity based on the ? rm’s net income in period n+1 (i. . , year 11). This formulation implies that the ? rm’s growth opportunities cease after that point. Depending on the ? rm and industry, eleven years may be an overor underestimate. Unfortunately, we do not have any ? rm-level data to construct more precise measures. Moreover, even if we had richer data there is no clearly preferred method for calculating a ? rm’s terminal value, as noted by Brealey and Myers (1996) (p. 78). We follow their suggestion to use this particular method because it “forces managers to remember that sooner or later the competition catches up. The second variant of real Qit , which we call “long-run real Q”, uses only two-yearahead earnings and long-term growth forecasts: Long Run Real Qit = Real Qit ? ?ECFit . (10) By excluding the one-year-ahead forecasts we can examine whether investment responds more to near-term or longer-run expectations of pro? tability. Also, this measure addresses the concern that real Q could capture liquidity e? ects because its ? rst term (? ECFit ) is highly correlated with realized period-t cash ? ow, our proxy for changes in internal net worth. Using long-run real Q gives cash ? ow the best possible chance to a? ct investment in our regressions. Our approach to constructing measures of fundamentals is an alternative to the VAR-based methods used by Abel and Blanchard (1986) and Gilchrist and Himmelberg (1995, 1999). Abel and Blanchard (1986) derive a linear approximation to Q, and then use a VAR estimated with aggregate data for US manufacturing to project the future discount rates and marginal returns to capital that appear in the approximation. Gilchrist and Himmelberg apply a variant of this technique to ? rm-level panel data. Our approach sidesteps the need for a VAR by relying on the analysts to project future earnings.
However, the VAR-based methods and our approach both invoke restrictive assumptions — 10 most notably, the assumption of quadratic adjustment costs, which delivers the linear relationship between investment and Q. To examine whether this assumption a? ects our results, a previous version of this paper estimated a semiparametric version of the model that allows q to a? ect investment nonlinearly. We omitted these results because the discussion of the semiparametric estimator is relatively involved and our empirical results were essentially the same as those presented here, giving us con? ence that the strong assumptions we invoke to construct real Q and its variants are not driving our results. A number of variables could be used to proxy for changes in internal net worth. We follow the bulk of the literature by using the ratio of current cash ? ow, de? ned as the sum of net income and depreciation, to beginning-of-period capital, CFit /Ki,t? 1 . 12 Thus, the equation we estimate is: Iit 1 CFit = ? + Qit + ? + ? it , Ki,t? 1 ? Ki,t? 1 (11) where Qit represents either Tobin’s Q, real Q, or one of the variants of real Q. The test for liquidity constraints with this equation is straightforward.
If the estimate of ? is positive and statistically signi? cant, we would conclude that some form of liquidity constraint is currently binding, as ? rms evidently invest out of cash ? ow, even after controlling for fundamentals. In contrast, if ? is statistically insigni? cant from zero, we would conclude in favor of the null neoclassical model. Questions can be raised, however, about the power of this test to detect liquidity constraints when they actually exist. In that case, the expectations embedded in Tobin’s Q (or real Q and its variants) could well include the anticipated e? cts of liquidity constraints, so that these variables would not be pure measures of fundamentals. Accordingly, Q might fully explain investment spending, leaving no role for cash ? ow. There is, no doubt, an element of truth in this concern. However, Chirinko (1997) showed that, in the presence of ? nancing constraints, Q generally is not a su? cient statistic for investment. Financial variables, such as cash ? ow or the interest coverage 12 Actually, the literature’s focus on current-period cash ? ow puzzles us, since marginal q includes the cash ? ow generated during the rst period in which the investment good is in service (see equation (4)). Indeed, this term should receive the largest weight in the calculation of q. Nonetheless, we used currentperiod cash ? ow to maintain comparability with prior work. In an earlier version of this paper we also used previous-period measures of liquidity. Our conclusions are una? ected when using this timing. 11 ratio, will also a? ect investment whenever the ? rm’s cost premium for external funding depends on its current earnings. This dependence seems quite plausible, as investors will be less concerned about the prospect of ? ancial distress — and the associated costs — for ? rms generating substantial current pro? ts. Thus, cash ? ow should be expected to in? uence investment in equation (11) for constrained ? rms. Those who believe otherwise should recognize that they are impugning not only our approach but all the investment-cash ? ow regressions reported in previous research. We estimate equation (11) using OLS and GMM. The OLS results will be biased and inconsistent to the extent that the current-period regressors are correlated with the error term. We present these results despite their econometric problems so that our ? dings can be compared to the numerous prior studies that have employed OLS. Our primary estimator is GMM, which yields consistent estimates provided that the instruments are uncorrelated with the error term. We use a variety of instrument sets — including some that contain analysts’ earnings forecasts — to examine whether the results are sensitive to the choice of instruments. Prior to estimation, we ? rst-di? erence equation (11) to remove the ? rm-speci? c error component, ? i , and introduce time dummies as regressors for ? t in each period. When it is serially uncorrelated, its ? rst-di? erence is MA(1), in which case lagged endogenous ariables dated at t ? 2 and earlier are valid instruments for the di? erenced equation. If the model is misspeci? ed the error term may display higher-order serial correlation, in which case even instruments dated at t ? 2 and before may be invalid. We test the validity of each instrument set in two ways. First, we report the p-value of the m2 test proposed by Arellano and Bond (1991) to detect higher-order serial correlation in the residuals. 13 Second, we report the p-value of the Sargan statistic (also know as Hansen’s J-statistic), which tests the joint null hypothesis that the model is correctly speci? d and that the instruments are valid (for further details see, e. g. , Arellano and Bond 1991; Blundell, Bond, Devereux, and Schiantarelli 1992). 14 Unfortunately, it is 13 The m statistic, which has a standard normal distribution under the null, tests for nonzero elements 2 on the second o? -diagonal of the estimated serial covariance matrix. We also tested, but (to conserve space) do not report, whether the ? rst o? -diagonal has nonzero elements. Since ? rst-di? erencing should introduce an MA(1) error we were not surprised to ? nd that we rejected the null of no ? st-order serial correlation in virtually every case. 14 Formally, the Sargan statistic is a test that the overidentifying restrictions are asymptotically distributed 2 ? (n? p) , where n is the number of instruments and p is the number of parameters. 12 not possible to test either hypothesis separately. Thus, considerable caution should be exercised in interpreting why the null is rejected — the instruments may be invalid due to serial correlation in the residuals, the model may be misspeci? ed, or both problems may be present. In summary, our empirical framework extends the usual method for estimating investment-cash ? w regressions by using Tobin’s Q and real Q as alternative controls for fundamentals and by using a variety of instrument sets in the GMM estimation. We employ this framework to assess the information content of analysts’ earnings forecasts and to evaluate the robustness of evidence for capital market imperfections from prior studies. 3 Data We estimate the model using ? rm-level data from two sources. The data on investment, the capital stock, Tobin’s Q, and cash ? ow, and the variables used to split the sample are from Compustat, while the data on expected earnings are from I/B/E/S International Inc.
We brie? y discuss the Compustat data and then describe in greater detail the I/B/E/S data. 3. 1 Compustat Dataset The Compustat dataset is an unbalanced panel of ? rms from the industrial, full coverage, and research ? les. The variables we use are de? ned as follows. The replacement value of the capital stock is calculated using the standard perpetual inventory method with the initial observation set equal to the book value of the ? rm’s ? rst reported net stock of property, plant, and equipment (data item 8) and a ? rm-level rate of economic depreciation constructed using the method in Cummins et al. (1994).
Gross investment is de? ned as the direct measure of capital expenditures in Compustat (data item 30). Cash ? ow is the sum of net income (data item 18) and depreciation (data item 14). Both gross investment and cash ? ow are divided by the beginning-of-period replacement value of the capital stock. The construction of tax-adjusted Tobin’s Q is discussed in detail in appendix A. The implicit price de? ator (IPD) for total investment for the ? rm’s 13 three-digit SIC code is used to de? ate the investment variable and in the perpetual inventory calculation of the replacement value of the ? rm’s capital stock.
The three-digit IPD for gross output is used to de? ate cash ? ow. These price de? ators are obtained from the NBER/Census database (http://www. nber. org/nberprod). We use Compustat data on the ? rms’ S&P bond rating and dividend payouts to split the sample, isolating those ? rms that may a priori face ? nancial constraints. 3. 2 I/B/E/S Dataset We employ data on expected earnings from I/B/E/S International Inc. , a private company that has been collecting earnings forecasts from securities analysts since 1971. To be included in the I/B/E/S database, a company must be actively followed by at least one securities analyst, who agrees to rovide I/B/E/S with timely earnings estimates. According to I/B/E/S, an analyst actively follows a company if he or she produces research reports on the company, speaks to company management, and issues regular earnings forecasts. These criteria ensure that I/B/E/S data come from well-informed sources. The I/B/E/S earnings forecasts refer to net income from continuing operations as de? ned by the consensus of securities analysts following the ? rm. Typically, this consensus measure removes from earnings a wider range of non-recurring charges than the “extraordinary items” reported on ? ms’ ? nancial statements. For each company in the database, I/B/E/S asks analysts to provide forecasts of earnings per share over the next four quarters and each of the next ? ve years. We focus on the annual forecasts to match the frequency of our Compustat data. In practice, few analysts provide annual forecasts beyond two years ahead. I/B/E/S also obtains a separate forecast of the average annual growth of the ? rm’s net income over the next three to ? ve years — the so-called “long-term growth forecast” which we denoted above as EGRit .
When calculating their forecasts of long-term growth, I/B/E/S instructs analysts to ignore the current state of the business cycle and to project, instead, the expected trend growth of the company’s earnings. Thus, the long-term growth forecast should contain information not in the one-year-ahead and two-year-ahead forecasts, which necessarily will be a? ected by current conditions. And for companies that make investment decisions based on the expected long-term returns to capital — in accord 14 with the neoclassical model — the long-term growth forecast should be an important determinant of investment.
We abstract from any heterogeneity in analyst expectations for a given ? rm-year by using the mean across analysts for each earnings measure (which I/B/E/S terms the “consensus” estimate). We multiply the one-year-ahead and two-year-ahead forecasts of earnings per share by the number of shares outstanding to yield forecasts of future earnings levels. As noted above, we generate the variables ECFit and ECFi,t+1 by scaling these forecasts of net income in periods t and t + 1 by the replacement value of the capital stock at the beginning of period t.
The one-year-ahead and two-year-ahead forecasts are available from 1976 but the long-term growth forecasts were not collected until 1981, which constrains the starting point of our sample. The data coverage increases gradually over time, with the Compustat universe largely covered by 1994. At the end date of our sample, December 1995, the I/B/E/S database included about 5,000 US corporations that were actively followed by securities analysts, plus nearly as many defunct companies that were previously covered. An important issue concerns the dating of the I/B/E/S earnings forecasts.
Shortly after the end of a ? rm’s ? scal year, securities analysts send I/B/E/S an initial forecast of earnings for the ? scal year that has just begun and for the next ? scal year. These are what we have called the one-year-ahead and two-year-ahead forecasts. As the ? scal year progresses, analysts process new information and ? le revised forecasts with I/B/E/S, yielding a sequence of one-year-ahead and two-year-ahead consensus forecasts for the ? rm. Similarly, I/B/E/S posts a sequence of consensus long-term growth forecasts over the ? scal year. We use the ? st forecast in each sequence. 15 By relating investment in year t to earnings forecasts issued at the beginning of the year, we reduce the risk of using more information than the ? rm actually has when it determines investment spending for the year. 16 15 The ? rst forecast is within 2 months of the beginning of the ? scal year for 75 percent of our sample and within 3 months for 97 percent of our sample. 16 With time-to-build lags, however, investment in year t may have been determined in large part or completely by information available before the start of year t.
In this case, the GMM results we present are consistent as long as the time-to-build lags do not exceed two years since we use an instrument set containing earnings forecasts formed at the beginning of year t ? 2 and earlier. 15 Our working assumption is that I/B/E/S earnings forecasts provide valuable information about the expected returns to investment. The empirical results in the next section support this view, as does a large literature on the properties of earnings expectations. 17 Nonetheless, analysts’ forecasts may not contain all available information.
While some studies have failed to reject rationality (see, e. g. , Keane and Runkle 1998), others have found that analysts’ forecast errors are predictable (see, e. g. , Brown 1996a). For our purposes, full rationality is not crucial; the I/B/E/S forecasts will have value as long as they provide a better proxy for fundamentals than do Tobin’s Q and its lags, which we show to be the case. 3. 3 Data Samples Used for Estimation We construct two samples from the ? rm-level data. The ? rst, which represents our primary sample, includes all ? rms with at least four consecutive years of complete Compustat and I/B/E/S data.
We require four years of data to allow for ? rst-di? erencing and the use of lagged variables as instruments. We determine whether the ? rm satis? es the four-year requirement after deleting observations that fail to meet a standard set of criteria for data quality (described below). The second, and larger, sample is constructed without regard for the availability of the I/B/E/S earnings expectations. It contains all annual observations for ? rms with at least four consecutive years of complete Compustat data — again, after imposing standard deletion rules.
This larger sample is intended to approximate the datasets used in previous research, which were not limited to ? rms with analyst coverage. 18 We deleted observations for the following reasons (the percent of the primary sample that the rule deletes is in parentheses): (1) the ratio of investment to beginning-ofperiod capital is greater than unity or less than zero (14 percent); (2) tax-adjusted Q is less than -1, its theoretical minimum, or greater than 30 (5. 5 percent); (3) real Q is less than zero or greater than 30 (2 percent); and, ? nally, (4) we also deleted the ? st and 17 For surveys of the literature see Coggin (1990); and Brown (1993, 1996a); Givoly and Lakonishok (1984). For an annotated bibliography covering more than 400 articles on earnings expectations see Brown (1996b). 18 The requirement that each ? rm be in the panel for at least four years eliminates about 21 percent of the potential observations for the primary sample and about 19 percent of those for the Compustat-only sample. 16 last half-percentiles in CF /K. 19 These types of rules are common in the literature and we employ them to maintain comparability to previous studies; in section 4. we discuss how our results are a? ected when we use di? erent cut-o? s. The ? rst and fourth cut-o? s are intended to eliminate observations that re? ect especially large mergers, extraordinary ? rm shocks, or Compustat coding errors. The second and third rules are intended to remove ? rms for which fundamentals may be seriously mismeasured. 4 Empirical Results 4. 1 Sample Statistics Table 1 provides the mean, median and standard deviation for the key variables in the two samples that we use. Column 1, labeled “Compustat”, presents summary statistics for the larger sample that consists of ? ms with the necessary Compustat data, irrespective of whether I/B/E/S data are available. Column 2, labeled “I/B/E/S”, refers to the primary sample for our empirical work, which includes ? rms for which we have the required data from both Compustat and I/B/E/S. The remaining columns refer to splits of the two samples. As shown in column 2, the median ? rm in our primary sample is mid-sized, with real (1992 dollar) sales of $764 million, and has been expanding fairly rapidly. This is evident from both the median growth rate of real sales (4. percent annually) and the high median ratio of annual investment outlays to beginning-of-period capital stock (0. 26). In addition, the ? nancial markets evidently believe that the median ? rm — with a tax-adjusted Tobin’s Q that exceeds 2. 6 — has valuable investment opportunities. 20 However, as indicated by the large standard deviation for each variable, our sample includes a broad range of ? rms with regard to size, investment behavior, and ? nancial health. 19 For comparison the ? rst exclusion rule deletes about 16 percent of the Compustat-only sample, the second about 6. percent, and the fourth also one percent. 20 The median value of real Q, at 0. 98, is less than half that of tax-adjusted Tobin’s Q. Recall that we constructed real Q from analyst expectations of earnings net of interest payments. Thus, the returns to debt holders are omitted from the numerator of real Q, causing it to be smaller than Tobin’s Q, which captures all of the ? rm’s liabilities. 17 Our primary sample omits about 25 percent of the nearly 12,000 observations in the Compustat sample (column 1), owing to the absence of I/B/E/S data.
We were concerned that these omissions might make this sample unrepresentative of the Compustat universe — and, in particular, skew it away from the ? rms often thought to be liquidity constrained. However, as can be seen by comparing columns 1 and 2, the Compustat and I/B/E/S samples have similar characteristics. Indeed, the means, medians and standard deviations of all variables except sales are nearly the same across the two samples. The ? rms in the I/B/E/S sample are somewhat larger than those in the Compustat sample (median real sales of $764 million versus $510 million).
Nonetheless, about 40 percent of the observations in the I/B/E/S sample are drawn from ? rms with real sales below the median value of the Compustat sample, indicating that the I/B/E/S/ sample does not seriously underweight smaller ? rms. One might still be concerned that the two samples may not match up after they are partitioned in standard ways. The remaining columns in the table show that this concern appears unwarranted as well. Focus, for example, on columns 9 and 10, which summarize the data for ? rms that lacked a bond rating in the prior year.
The di? erences across the Compustat and I/B/E/S samples are slight, except for the somewhat larger size of the median ? rm in the I/B/E/S sample ($361 million in real sales, versus $252 million for Compustat ? rms). However, the I/B/E/S sample largely preserves the size di? erence between rated and unrated ? rms that is evident in the Compustat sample. If unrated ? rms (within the Compustat universe) really do face greater liquidity constraints than ? rms with rated bonds, we should be able to detect this pattern with our I/B/E/S sample.
As another check we constructed the aggregate ratios of investment to beginning-ofperiod capital for the I/B/E/S and Compustat samples. We then regressed the aggregate Compustat ratio on the aggregate I/B/E/S ratio; the R 2 from this regression is the total variation in the Compustat ratio explained by the I/B/E/S ratio. This regression yields an estimated slope coe? cient of 0. 876 with a standard error of 0. 078 and an R 2 = 0. 927. In ? rst di? erences the same regression yields a coe? cient estimate of 1. 000 with a standard error of 0. 120 and an R 2 = 0. 886. In both regressions the intercepts are statistically insigni? ant from zero. The nearly one-for-one movement in these ratios 18 indicates that the I/B/E/S sample and the broader Compustat sample display about the same investment behavior over time. 4. 2 OLS Estimation Results To begin our empirical analysis, Table 2 presents OLS estimates of the ? rst di? erence of equation (11) using two di? erent variables to control for fundamentals: tax-adjusted Tobin’s Qit and real Qit , constructed using the I/B/E/S earnings forecasts. The top panel reports estimates obtained from the Compustat sample, while the middle and bottom panels report estimates from the I/B/E/S sample.
The dependent variable for all regressions is the ? rst di? erence of the ratio of investment to beginning-of-period capital, and the explanatory variables always include a full set of year dummies and a constant term. 21 Focusing on the top panel, column 1 reports the estimates from a regression with Tobin’s Q and the ratio of cash ? ow to beginning-of-period capital as explanatory variables. This regression has been estimated in many previous studies. As is typically found, the coe? cient on Tobin’s Q is positive and statistically signi? cant, but very close to zero (0. 16 in our case); this estimate implies marginal adjustment costs that are implausibly high — more than $5 for a $1 investment. The coe? cient on CFit /Ki,t? 1 is strongly signi? cant, though its value (0. 15) is at the lower end of the range of previous estimates. Scanning across columns 2 through 5, the same pattern holds for our two sets of sample splits: Small but signi? cant coe? cients on Tobin’s Q (ranging from 0. 012 to 0. 029) and signi? cant coe? cients on cash ? ow (ranging from 0. 11 to 0. 19). Consistent with other studies, we estimate the cash-? ow coe? ient to be significantly larger for unrated ? rms than for those with a bond rating. However, ? rms that paid no dividend in the prior year have a smaller cash-? ow coe? cient than do dividend-paying ? rms, contrary to the presumption that low-dividend ? rms are ? nancially constrained. This result does not concern us, in part because there is already con? icting evidence in the literature regarding dividend splits. For example, while 21 The careful reader will notice that the number of ? rms in each of the two-way sample splits is less than the total number of ? ms in the ? rst column. The requirement that the ? rm have four consecutive years of data means that we lose some ? rm-year observations when ? rms change status (e. g. , begin paying dividends toward the end of the sample period). 19 Fazzari et al. (1988) estimated that investment by low-dividend ? rms was relatively sensitive to cash ? ow, Gilchrist and Himmelberg (1995) found the reverse. Moreover, the theoretical results in Kaplan and Zingales (1997) and Chirinko (1997) cast doubt on the whole premise underlying such comparisons by showing that the size of cash-? ow coe? ients need not have a monotonic relation with the severity of ? nancial constraints. The intuition is that the sensitivity of investment to cash ? ow also depends on the speci? cs of the ? rm’s production technology. Our results from the dividend split may simply illustrate this point. The middle panel presents the results obtained by estimating the same regression on the I/B/E/S sample. The standard errors on the coe? cient estimates generally increase in size — as would be expected with the switch to a smaller sample — but the estimates themselves are quite similar to those in the top panel.
This similarity is reassuring because we have no choice but to use the I/B/E/S sample once we introduce the analysts’ earnings expectations either through real Q or as instruments. The bottom panel shows the e? ect of substituting real Q for Tobin’s Q, while keeping everything else unchanged from the middle panel. The overall ? t of the regression improves, as indicated by the higher R 2 in every column except one. In addition, the coe? cient on real Q is highly signi? cant, demonstrating that the earnings expectations embedded in real Q do convey useful information about investment spending. 2 Even more striking, the cash-? ow coe? cient is much smaller than in the middle panel — ranging now from just 0. 015 to 0. 057 — and is statistically signi? cant in just two of the ? ve columns. These results raise questions about the liquidity e? ects found in studies that have used Tobin’s Q to control for fundamentals. When we substitute a simple linear function of analysts’ earnings expectations, which arguably contain less noisy information concerning ? rms’ true neoclassical fundamentals, we ? nd much less evidence of liquidity e? ects.
However, the OLS results presented in table 2 and in previous studies will be biased if, as seems likely, the explanatory variables are correlated with the error term. Thus, our OLS results are nothing more than a ? rst pass at the data that allows 22 The larger coe? cient on real Q arises, in part, because real Q is typically only one-half to one-third the size of Tobin’s Q and varies within a narrower range (see Table 1). 20 us to connect with prior work. We now turn to GMM estimation to circumvent the potential bias in the OLS estimates and to test whether the strong assumptions needed to construct real Q in? ence the results. If internal funds are unimportant in table 2 because analysts’ forecasts truly measure fundamentals better than has been done in the past — and not simply because of the restrictive assumptions behind real Q — then we should obtain similar results when we use the analysts’ forecasts as instruments for Tobin’s Q and real Q. 4. 3 GMM Estimation Results Table 3 provides the GMM estimates of the ? rst-di? erenced investment equation using the I/B/E/S sample and either tax-adjusted Tobin’s Q or real Q as the control for fundamentals. We implement GMM with two alternative sets of instrumental variables.
The upper panel displays the results for an instrument set that includes the period t ? 2, t ? 3, and t ? 4 values of I/K, tax-adjusted Tobin’s Q, and CF /K, as well as a full set of year dummies and a constant (which are included in all instrument sets). With this instrument set, the coe? cients on Tobin’s Q (shown in the odd-numbered columns) are small and statistically insigni? cant, while the coe? cients on cash ? ow are large (ranging from 0. 229 to 0. 378) and highly signi? cant in all samples except the no-dividend group, where the estimate is signi? cant at the 10 percent level.
Despite the sizable cash-? ow coe? cients, these results should not be taken as evidence for the presence of liquidity constraints. Most notably, every set of estimates fails the Sargan test. This means that the model is misspeci? ed, the instruments are invalid, or both. As another sign of econometric problems, the m2 test provides evidence of serial correlation in the residuals in two of the ? ve cases. 23 The even-numbered columns show the e? ect of replacing Tobin’s Q with real Q as the control for fundamentals. As shown, the coe? cient on real Q is signi? ant in all cases except one, in contrast to the uniform insigni? cance of Tobin’s Q. In addition, the coe? cient on cash ? ow turns negative in three cases, and is never statistically 23 We would also note that the sample splits fail to produce signi? cantly larger cash-? ow coe? cients for the no-dividend and unrated ? rms than for other groups. Many would regard this result, by itself, as evidence against liquidity constraints. However, we would take a more agnostic stand, given the theoretical work, discussed above, that cautions against trying to infer whether liquidity constraints exist by comparing cash-? w sensitivities across sample splits. 21 signi? cant. These estimates certainly do not support a liquidity e? ect on investment. But we would not rely on these results, as they also fail the Sargan test virtually across the board (although the residuals show less evidence of serial correlation). One possible explanation for the pattern of results in the top panel is that the instruments are weaker for Tobin’s Q than for real Q, which could allow cash ? ow to have a greater e? ect on investment in the Tobin’s Q regression. However, the instruments for Tobin’s Q are actually quite powerful.
For example, in the full I/B/E/S sample, the F -test for the joint insigni? cance of the full set of instruments in the “? rst-stage” regression has a p-value below 0. 0001. Applying the same test to the “? rst-stage” regression for real Q also yields an in? nitesimal p-value. Thus, weak instruments do not appear to be driving our results. Another possible explanation focuses on serially correlated measurement error in Tobin’s Q — resulting, perhaps, from persistent deviations of asset prices from their fundamental value. This would make lags of Tobin’s Q inadmissible as instruments.
To test this hypothesis, we drop lags of Tobin’s Q from the instrument set, and replace them with lags of another variable that should help measure the ? rm’s “fundamentals”, the ratio of sales to beginning-of-period capital, Y /K. In all other respects, this instrument set is the same as the prior one. As shown in the lower panel, this seemingly minor change to the instrument set has a considerable e? ect on the estimates. The coe? cients on Tobin’s Q and real Q are dramatically larger than those in the upper panel, and they are almost always signi? cant. The estimates of the cash-? ow coe? ient vary widely across the columns of the table, but the only statistically signi? cant one is negative; this contrasts with the positive, signi? cant coe? cients shown in the upper panel when we used Tobin’s Q as the control for fundamentals. In addition, the Sargan test is now not rejected (at the ? ve percent level) in eight of ten cases. The m2 test for serial correlation is also not rejected in eight of ten cases. Accordingly, we have more faith in these estimates than those presented in the upper panel or in table 2. 24 As a check on our results, we repeated the GMM estimation on the larger Compustat sample.
Table 4 reports these results, omitting the speci? cations that involve real 24 One might be concerned that the “fundamental” instruments are weak. However, this is not the case. In the full I/B/E/S sample, the F -test of this instrument set for both Tobin’s Q and real Q has a p-value below 0. 0001. 22 Q, which we cannot calculate for every ? rm in this sample. Although the coe? cient estimates vary somewhat across the two tables, the basic conclusions are the same. In particular, with lags of Tobin’s Q in the instrument set (the upper panel), we again generate positive and (mostly) signi? cant cash-? w coe? cients but fail the Sargan and m2 tests in all cases. When we remove lags of Tobin’s Q from the instrument set and replace them with lags of the sales-capital ratio (the lower panel), the coe? cient on Tobin’s Q jumps to values that are economically and statistically signi? cant. The coe? cient estimates on cash ? ow — while sometimes large — become uniformly insigni? cant, and the Sargan and m2 tests now fail in roughly half the cases rather than across the board. Hence, as in table 3, the estimates with the more desirable econometric properties provide no evidence of credit constraints.
Looking at tables 3 and 4 together, it’s startling that the statistical and economic properties of the estimates improve so dramatically when we do nothing more than remove the lags of Tobin’s Q from the instrument set. To our knowledge, no other investment study has undertaken this simple experiment, the results of which raise questions about the evidence for liquidity constraints from a number of other investment papers. We discuss the existing literature in more detail after we present the rest of our econometric results.
The results presented so far highlight the importance of choosing instruments that contain considerable information about the ? rm’s fundamentals and that have desirable statistical properties. By these criteria, analysts’ earnings expectations are obvious candidates as instruments. Accordingly, we created a larger instrument set that includes the period t? 2, t? 3, and t? 4 values of I/K, CF /K, Y /K, the ratios of the analysts’ forecasts of one-year-ahead and two-year-ahead earnings to beginning-of-period capital, and the long-term growth forecast.
The top panel of table 5 reports the GMM estimation results with this larger instrument set. In all other respects, the estimation method and data are identical to those used to generate the results in the bottom panel of table 3. As can be seen, the coe? cients on Tobin’s Q and real Q are somewhat smaller than those shown at the bottom of table 3, though they remain signi? cant in most cases. The coe? cients on CF /K are all insigni? cant, as they were with the smaller instrument set. However, the performance 23 with respect to the Sargan test has deteriorated, with the model now being rejected in seven of the ten columns.
The middle panel examines how the results change when we omit CF /K and Y /K from the instrument set, while leaving in the lags of analyst expectations and I/K. As shown, the point estimates are quite similar to those in the lower panel of table 3: the coe? cients on Tobin’s Q and real Q are large and statistically signi? cant, while those on CF /K are insigni? cant. Using this instrument set, however, yields more precise coe? cient estimates on Tobin’s Q and real Q, as we would expect if lagged earnings expectations are more informative measures of the determinants of investment than lagged accounting variables.
Moreover, we ?nd almost no evidence of model misspeci? cation from the Sargan test or the m2 test for serial correlation. In fact, comparing these results with those at the bottom of table 3, the statistical properties of the model improve when the analyst expectations replace the “fundamental” variables in the instrument set. If ? rms make investment decisions based on the expected long-term returns to capital — in accord with the neoclassical model — the two-year-ahead and long-term growth forecasts should contain the most information about the fundamentals.
To test this idea, the bottom panel reports the results obtained when we omit the one-year-ahead expectations from the instrument set in the middle panel. The coe? cients on Tobin’s Q and real Q are similar to those in the middle panel, and they are uniformly signi? cant, despite some increase in their standard errors. The coe? cient on CF /K remains insigni? cant in all cases. These estimates con? rm that, indeed, it is the longer-range projections that drive our results. Moreover, the one-year-ahead forecasts may not be valid instruments, owing to correlation with the contemporaneous error term.
As shown in the bottom panel, when these forecasts are removed from the instrument set, we no longer reject the Sargan test at the ? ve percent level for any speci? cation. We can use the estimates on Tobin’s Q and real Q in the middle and bottom panels of table 5 to calculate the range of implied elasticities of the investment-capital ratio with respect to the fundamental variable. For both Tobin’s Q and real Q the elasticity is always above unity when evaluated at median values of the variables; the elasticity is 25 to 50 percent larger when evaluated at means.
These estimates indicate that investment spending is highly sensitive to fundamentals. The estimates also imply that marginal 24 adjustment costs for a $1 investment are all less than $1, evaluated at either the means or medians of the sample variables. Table 6 addresses two potentially important concerns about the results obtained with real Q as the control for fundamentals. First, the analysts’ one-year-ahead forecasts built into real Q are highly correlated with our liquidity variable, which could reduce the power of tests to identify liquidity e? ects if they actually exist.
To address this concern, table 6 reports GMM estimates obtained with long-run real Q from equation (10) as the control for fundamentals; recall that long-run real Q removes the one-period-ahead forecasts, ECFit , from our construction of real Q. The second concern about the I/B/E/S forecasts is that they have a ? nite horizon, and thus fail to impound the full return to long-lived investment. To address this concern, we report the results obtained with another variant of real Q — the terminal-value real Q shown in equation (9), which adds an estimate of the residual value from the period beyond our forecast horizon.
The odd-numbered columns report the results when we use long-run real Q in place of real Q. In all other respects, the speci? cation is identical to that in the middle panel of table 5. As can be seen, the coe? cients on long-run real Q are all statistically signi? cant, while the cash-? ow coe? cients remain uniformly insigni? cant. The Sargan test is not rejected in four of the ? ve columns, and there is no evidence of second-order serial correlation. The results are strikingly similar to those in the middle panel of table 5, showing that the presence of one-period-ahead forecasts in real Q does not bias us against ? ding liquidity e? ects. 25 The coe? cient estimates on terminal-value real Q, in the even-numbered columns, are smaller than those on real Q in the middle panel of table 5, likely because the mean of terminal-value real Q is substantially greater than 25 These results rule out the following interpretation of investment behavior suggested to us by Owen Lamont. Suppose the ? rm plans its investment spending with a one-year lead and follows a rule of thumb under which its period t investment re? ects its expected cash ? ow in that period: CFit Iit = ? + ? Et + ? it , Ki,t? 1 Ki,t? where Et is the expectation operator that uses beginning-of-period information. If this were the true model but we instead estimated equation (11) using real Q (which, by construction, contains Et CFit /Ki,t? 1 ), the estimated coe? cient on real Q would tend toward ? , and the estimate of the cash-? ow coe? cient would tend toward zero if realized CFit were noisy. However, if we estimated equation (11) using long-run real Q — which does not contain forecasts of period t cash ? ow — we would ? nd that the coe? cient on long-run real Q tended toward zero, while that on realized CFit /Ki,t? would equal ?. Since we ? nd that the results are virtually identical using real Q and long-run real Q, we can reject this interpretation of the data. 25 that of real Q. However, the coe? cients on terminal-value real Q are all statistically signi? cant and we again ? nd no signi? cant cash-? ow e? ects. In interpreting our results, one could ask whether real Q explains investment well simply because the analysts are privy to inside information about the ? rm’s spending plans. If so, real Q would impound everything that a? e
