Copyright Impacts on Relative Firm Sales: Evidence from the National Football League *

Transcription

1 Copyright Impacts on Relative Firm Sales: Evidence from the National Football League * Daniel J. Slottje Professor Southern Methodist University Daniel L. Millimet * Assistant Professor Southern Methodist University Michael J. Buchanan KPMG, LLP August 2003 Abstract Using panel data on the rankings of merchandise sales for NFL franchises from , we analyze the effect of copyrights (in this case, team logo) using several econometric methods: OLS, GLS, fixed effects models, Arellano and Bond's (1991) dynamic fixed effects estimator, and Rosenbaum and Rubin's (1983) propensity score matching estimator. Despite the fact that logo changes are costly to undertake and improved merchandise sales is the most likely motivator for incurring such costs, the preponderance of evidence indicates that logo changes do not impact sales rankings. JEL: C14, C23, L83, M31 Key words: Copyright, Merchandise sales, Dynamic panel estimation, Propensity score * Correspondence to: Daniel Millimet, Southern Methodist University, Department of Economics, Box 0496, Dallas, Texas ; phone: (214) ; fax: (214) ; millimet@mail.smu.edu.

2 1. Introduction In the current changing business landscape, it is becoming increasingly necessary for firms to understand what their intellectual property holdings are (e.g., Curry, 1998; Jaffe, 2000). In this paper, we explore the impact of one form of intellectual property, copyrights, on relative firm sales. Title 17 of the United States Code Section 102 defines a copyright as: " original works of authorship fixed in any tangible medium of expression, now known or later developed, from which they can be perceived, reproduced or otherwise communicated, either directly or with the aid of a machine or device This includes pictorial, graphic and sculptural works." The copyright we focus on herein are firm logos, in particular the logos of franchises in the U.S. National Football League (NFL). NFL logos clearly fall within the scope of copyrights as defined in Section 102 of Title 17. NFL franchises possess a number of assets, any of which may be affected by copyrights: concessions from the franchises' home cities (e.g., tax funds to defray stadium costs), luxury box and general ticket sales, players, etc. While merchandise sales are presumably most likely to be affected by franchise logos, the NFL treats the magnitude of actual sales of team merchandise as proprietary information and it is not available for public consumption. For that reason, previous work in Slottje et al. (2002) analyzed the impact of NFL logos on total franchise value, as well as demand for firm output as measured by ticket sales, finding a negative effect of logo changes on franchise value and a positive, but not robust, impact on ticket sales. Since the production of new logos involves an enormous sunk cost, and (most) NFL franchises are no different than firms in other sectors in that profit-maximization is the prime motivator, the inability to detect a beneficial impact of such an undertaking in Slottje et al. (2002) is surprising. However, if the primary franchise asset affected by logos is merchandise sales, then it could be that the positive effect of logos was missed by focusing on the highly

3 aggregated measure of total franchise value. Thus, in this paper, we revisit the issue of NFL franchise logos. Although data on actual merchandise sales is still not publicly available, relative rankings of team merchandise sales are available on an annual basis. The previous empirical literature in this area is extremely sparse. In addition to the study by Slottje et al. (2002), a few previous studies attempt to value patent rights held by firms in Europe using data on patents, patent renewals, and stock returns (e.g., Schankerman and Pakes, 1986; Pakes, 1985, 1986; Pakes and Simpson, 1989; Lanjouw 1998; Lanjouw et al., 1998). The logic in the patent literature is similar to that here: patent renewals are costly and therefore patents must confer some beneficial impact on firms if renewal decisions are guided by economic considerations. However, to our knowledge, empirical analysis of the value of copyrights is limited to Slottje et al. (2002). To estimate the impact of a logo change on subsequent relative firm sales, we utilize panel data from The copyright impact is empirically identified because of variation in the data that arises from teams periodically altering their logos. By changing logos, these teams provide a measurable event that can be assessed to see if new copyrights impact annual merchandise sales rankings. To assess the robustness of the results, we implement several econometric techniques. First, we utilize several straightforward parametric panel models, controlling for time invariant unobservable attributes of franchises that may be correlated with the decision to undertake logo changes as well as merchandise sales rankings. Second, because franchises ranking lower in total merchandise sales tend to reinvent their logo more often, we estimate Arellano and Bond's (1991) dynamic panel specification, explicitly controlling for lagged values of merchandise sales rankings as well as time invariant, franchise-specific attributes. Finally, we utilize a difference-in-differences (DID) semi-nonparametric propensity

4 score matching method. While matching methods are applicable primarily to problems of selection on observables, panel data allows us to employ a DID matching estimator, similar to that in List et al. (2002, 2003), to control for the presence of unobservables that under normal circumstances may lead to biased estimates. The results are surprising, but consonant with Slottje et al. (2002). Controlling for other determinants of merchandise sales in the NFL, particularly franchise success on the playing field, the preponderance of evidence fails to indicate a beneficial impact of new copyrights on relative firm sales. The remainder of the paper is organized as follows. Section 2 discusses the data and outlines the empirical methodology. Section 3 presents the results. Section 4 concludes. 2. Data and Methodology 2.1 Data The data set includes information on the 31 current NFL franchises and spans the period , and is identical to that used in Slottje et al. (2002). 1 As noted in that paper, because the NFL mandates revenue-sharing among the franchises for revenue raised obtained from merchandise sales, television contracts, etc., franchise-specific data on such sources of revenue are not publicly available. However, annual rankings of merchandise sales are available. Publicly available franchise-specific attributes available as controls are: whether or not the team has changed its logo from the preceding season, annual wins and losses, whether the team won or lost the Super Bowl in a given year, whether the franchise is new or relocated to a new city since the preceding season, the age of the franchise, the conference and division in which the team plays, and stadium capacity. Finally, we also utilize controls for the socio- 1 Data limitations prevent us from utilizing data prior to Moreover, the Houston Texans did not begin play until the season; thus, only 31 franchises.

5 economic characteristics of each franchise's home market: population, per capita income, and the local unemployment rate (obtained from the U.S. Bureau of Economic Analysis). Summary statistics, disaggregated by logo changers and non-changers, are provided in Table 1. Over the ten-year period analyzed, we observe 14 logo changes. As can be seen, logo changers on average have a higher ranking in terms of merchandise sales (18.5 versus 15.4). 2 In addition, in the year preceding the logo change, logo changes had a lower average ranking (13.2 versus 15.6). This is consonant with our intuition that logo changes are endogenous, reflecting low merchandise sales in the past. However, franchises with new logos were more successful measured in terms of victories on the playing field than those that did not reinvent their logos, winning an average of two additional games per year. In the year prior to the logo change, the average difference in victories between soon-to-be logo changers and non-changers was 0.3. Thus, one must be careful not to confound the effect of greater on-the-field success on relative merchandise sales with the impact of logo changes. 2.2 Parametric Approach To discern between the various determinants of relative firm sales, we begin with several parametric specifications. All specifications are nested in the following estimating equation: 1 Φ ( r ) = α + λ + L δ + X β + ε it i t it it it (1) where r it is the merchandise sales ranking (in percentile) of franchise i in year t; Φ is the standard normal cumulative distribution function (CDF); α are franchise fixed effects; i λ are t year fixed effects; L it is a binary variable taking a value of unity if a franchise changed its logo from the previous year, zero otherwise; X it is a vector of franchise attributes to be controlled. The variables in X include: won/loss record, controls for whether or not the team won the league 2 Throughout the analysis, a rank of one is assigned to the franchise with the lowest merchandise sales in a given

6 championship or made it into the league championship game that year, dummy variables for whether the team is a new franchise or relocated from a different city, the seating capacity of the team's home arena, and finally socio-economic characteristics of the franchise's home metropolitan area (population, mean per capita income, and unemployment rate in that city). The presence of Φ warrants explanation. Since rankings, r, follow a uniform distribution, the normality assumption utilized in the parametric specifications is clearly invalid. Consequently, a transformation is needed such that the normality assumption may be maintained. One such commonly used transformation involves the inverse standard normal CDF. Proceeding, the baseline specification restricts (1) by assuming that α = α for all i and i that ε is independent and identically distributed across observations. This reduces to a simple it pooled OLS regression. Next, we maintain the assumption of no franchise-specific heterogeneity, but we allow the error term to follow an AR(1) process. This is estimated by Feasible Generalized Least Squares (FGLS). The third specification allows each franchise to have a unique intercept and estimates (1) with fixed effects methods assuming the error term is well behaved. Finally, we re-estimate the fixed effects model allowing the error term to follow an AR(1) process. We focus on the potential autoregressive nature of the error terms since merchandise sales rankings are highly persistent over time (see Figure 1), most likely due to levels of fan support and other unobserved attributes affecting the determination of sales that change slowly from one season to the next. year. Thus, a higher ranking corresponds to greater sales.

7 2.3 Dynamic Panel Approach (GMM) An alternative specification is the dynamic panel model of Arellano and Bond (1991). 3 The benefit of this specification is that it explicitly conditions on lagged values of merchandise sales rankings, thereby controlling for the most likely source of endogeneity, while also controlling for unobserved franchise-specific heterogeneity. Thus, as opposed to allowing for autocorrelation in unobservable shocks to rankings (e.g., trends in the popularity of the franchise), the model explicitly allows past rankings to affect current rankings. The model uses first-differencing to remove time-invariant, franchise-specific attributes, and then uses twice-lagged (and higher orders) of the dependent variable as instruments. Specifically, the model is given by ~ r = α + λ + θr~ L X it i t it 1 + δ + β + it it ε (2) it where r ~ is the transformed merchandise sales ranking. First-differencing yields r ~ = λ + θ ~ r L X it t it 1 + δ + β + it it ε (3) it Assuming the errors, ε, are not autocorrelated, r it it 1 will still be correlated with the error ~ ~ term, ε it 1, in (3). However, r it 2, r it 3 hand, ε is autocorrelated (or, equivalently, it ~, etc. are available as instruments. If, on the other ε follows an AR(2) process or higher), then the it instruments will be invalid. Tests of autocorrelation and a Sargan test of the overidentifying restrictions are conducted, as in Arellano and Bond (1991). 2.4 Propensity Score Matching Method An alternative method of assessing the impact of a discrete treatment in this case, logo changes on (transformed) rankings of merchandise sales is the method of propensity score 3 See also Bond (2002).

8 matching developed in Rosenbaum and Rubin (1983). 4 The fundamental problem in identifying treatment effects is one of incomplete information. While one observes whether the treatment occurs and the outcome conditional on treatment assignment, the counterfactual is unobserved. Let y i1 denote the outcome of observation i if the treatment occurs (given by T i = 1); y i0 denotes the outcome in the absence of treatment ( T = 0 ). If both states of the world were observable, the average treatment effect, τ, would equal y1 y 0, where the former (latter) average represents the mean outcome for the treatment (control) group. However, given that only y 1 or y 0 is observed for each observation, unless assignment into the treatment group is random, generally τ y1 y 0. such that The solution Rosenbaum and Rubin (1983) advocate is to find a vector of covariates, Z, y y T, pr ( T = 1 Z) (0,1) (4) 1, 0 Z where denotes independence. If one is interested in estimating the average treatment effect, only the weaker condition is required. E[y 0 T = 1,Z] = E[y 0 T = 0,Z] = E[y 0 Z], pr ( T = 1 Z) (0,1) (5) For condition (5) to hold, the conditioning set Z should be multi-dimensional. Consequently, finding observations with identical values for all covariates in Z may be untenable. However, Rosenbaum and Rubin (1983) prove that conditioning on p(z) is equivalent to conditioning on Z, where p ( Z) = Pr( T = 1 Z) is the propensity score. p(z) is estimated via a standard probit model. i 4 See Blundell and Costa-Dias (2002) for a recent review of the method, as well as a comparison of the method to

9 Upon estimation of the propensity score, a matching algorithm must be defined in order to estimate the missing counterfactual, y 0i, for each treated observation i. The simplest algorithm is nearest-neighbor matching, whereby each treated observation is paired with the control observation whose propensity score is closest in absolute value (Dehejia and Wahba, 2002). 5 Unmatched controls are discarded and the average treatment effect on the treated (TT) is τ TT = E[y 1 T = 1, p(z)] - E[y 0 T = 0, p(z)] = E[y 1 - y 0 p(z)] (6) The estimator in (6) will provide an unbiased estimate of TT only if condition (5) is satisfied. As such, matching is useful as a solution to problems of selection on observables. However, we amend the basic matching algorithm in two important ways to utilize our panel data and remove certain unobservables that may not be controlled by simply conditioning on the propensity score. First, we restrict the pool of potential controls to which a given treated observation may be paired. Specifically, we perform the matching exercise twice: (i) unrestricted matching, and (ii) restricting matched pairs to be from the same year. By matching within-year, we explicitly remove any time-specific unobservables not already controlled for by the propensity score. Thus, the estimator in (6) becomes τ TT,t = E[y 1 T = 1, p(z), t] - E[y 0 T = 0, p(z), t] = E[y 1 - y 0 p(z), t] (7) where t indexes year. Second, we employ a difference-in-differences (DID) matching estimator, similar to that used in Heckman et al. (1997), Smith and Todd (2000), Eichler and Lechner (2002), and List et al. (2002, 2003). The strategy entails making an assumption of bias stability (BS) and requires panel data. The intuition is that although the condition in (5) may not hold due to the presence of other common econometric techniques. 5 Typically nearest-neighbor matching is performed with replacement, implying that a given control observation may be matched to multiple treatment observations. Dehejia and Wahba (2002) verify that matching with replacement fares at least as well as matching without replacement and possibly better.

10 unobservables correlated with the decision to undertake a logo change and current relative firm sales, the bias detected prior to the treatment may provide a reasonable estimate of the posttreatment bias. For notation, we define the DID counterpart to (6) and (7) as τ DID = τ TT - τ' TT τ DID,t = τ TT,t - τ' TT,t (8a) (8b) where τ' TT, τ' TT,t are the mean differences in lagged (transformed) merchandise sales rankings across the matched treatment and control groups in the unrestricted and restricted cases, respectively. Upon completing the matching estimation, balancing tests are conducted. Balancing refers to the fact that after conditioning on the propensity score and obtaining the matched subsample, the distribution of the conditioning variables, Z, should not differ across the treatment and control group. Thus, after matching, we also test for differences in the mean of the Z's. Finally, it is important to mention the differences between matching estimators and the estimators from the previous section. First, the matching estimator entails relatively few distributional assumptions. Second, matching estimators identify a restricted sub-sample of control observations that are most "similar" to the treatment group, whereas the previous models utilize all available observations. While this is a positive to the extent that controls deemed too different from the treatment group are excluded, since there are only 14 treated observations in the data, this leads to small samples. Third, matching allows for nonparametric interactions between all the covariates in Z in the determination of the outcome of interest (Bratberg et al. 2002). Finally, whereas the previous methods yield estimates of the average treatment effect (i.e., the expected effect of a logo change on the sales rankings of a randomly chosen observation), the matching method discussed herein yields an estimate of the average treatment

11 effect on the treated (i.e., the expected effect of a logo change on the sales rankings of a randomly chosen observation from the treatment group). 3. Empirical Results 3.1 Parametric Estimates The results from the four specifications detailed in Section 2.2 are presented in Table 2. The simple pooled OLS model (column 1) suggests a negative, but statistically insignificant effect of logo changes on relative merchandise sales. Victories and Super Bowl championships, however, are, as expected, positively related to merchandise sales rankings. In addition, newly relocated franchises and franchises that play in wealthier metropolitan areas also rank relatively higher in terms of merchandise sales. While the standard errors reported in column (1) are robust to arbitrary serial correlation within franchises, allowing the errors to specifically follow an AR(1) process (column 2) is more efficient if this error structure is correctly characterizes the data. Regardless, the results in column 2 do not alter the basic finding from the pooled OLS model that logo changes do not impact relative merchandise sales. The OLS fixed effects model with standard errors robust to arbitrary serial correlation within franchises (column 3) and the AR(1) fixed effects model (column 4) control for time invariant, unobservable franchise attributes (such as fan loyalty and national appeal). These specifications do not contradict the above finding: logo changes continue to have no impact on relative merchandise sales. In terms of the other control variables, victories, Super Bowl championships, Super Bowl losses, and being a new franchise are positively associated relative merchandise sales in column 3, while Super Bowl championships, Super Bowl losses, and home market population are statistically significant in column 4. In sum, the parametric models

12 suggest that the apparent positive effect of logo changes on relative merchandise sales discussed in section 2.1 is primarily attributable to the success of franchises on the field. 3.2 Dynamic Panel Estimates The results from Arellano and Bond (1991) GMM estimator are presented in Table 3. Four specifications are estimated: (i) conditioning on (one-period) lagged values of the dependent variable; (ii) conditioning on (one-period) lagged values of the dependent variable and measures of franchise success (i.e., wins and Super Bowl victories or defeats); (iii) conditioning on one-period lagged values of the dependent variables and one- and two-period measures of franchise success; and, (iv) conditioning on one- and two-period lagged values of the dependent variable and measures of franchise success. All specifications also include controls for the contemporaneous values of the remaining franchise attributes. In addition to reporting the most relevant coefficient estimates, we also report the results of the Sargan overidentification test and the test for no autocorrelation (in the non-differenced data). All four specifications in Table 3 continue to find a statistically insignificant effect of logo changes on merchandise sales rankings. Moreover, as suggested by Figure 1, sales rankings are found to be highly persistent over time as lagged values are positively related to current rankings in columns 1 3, as one would expect. Finally, the Sargan test and test for no autocorrelation indicate that all models are well specified with regards to the validity of the instruments and the assumptions concerning the nature of the error process. 3.3 Propensity Score Matching Estimates The final estimation technique is the propensity score matching method. The results are shown in Table 4. Column 1 (2) reports the mean differences between the matched treatment and control group using the unrestricted (within-year) matching algorithm. The average

13 difference in the propensity score across the matched pairs is 0.05 with unrestricted matching; 0.10 under within-year matching. Neither difference is statistically significant (unrestricted: p = 0.54; within-year: p = 0.22). In addition, we note that the differences between the matched treatment and control group in terms of the various observed attributes are never statistically significant at the 95% confidence level. Moreover, we never reject the null of joint equality of the means of the various control variables using a Hotelling T 2 tests (unrestricted matching: F = 0.38, p = 0.96; within-year matching: F = 0.34, p = 0.97). In terms of the estimated logo effect, relative merchandise sales is higher among those franchises that changed their logos using the unrestricted matching algorithm, although the difference is not statistically significant at conventional levels (p = 0.13). However, as stated previously, if assignment to the treatment group is based on unobservables not controlled for by matching on the propensity score and these unobservables are associated with merchandise sales, then the matching estimate of the average treatment effect will be biased. Thus, turning to the DID estimator suggests a positive and statistically significant effect of logo changes on relative merchandise sales (τ DID = 0.48, p = 0.06) despite the small sample size. Using the within-year matching algorithm (column 2), the DID estimate is of similar magnitude to the estimate in column 1, but is no longer statistically significant at conventional levels (τ DID,t = 0.39, p = 0.12). Which estimate is preferred? If time-specific unobservables are important, and these are not implicitly removed by the DID estimation, then the within-year matching estimates are preferable. On the other hand, if time-specific unobservables do not play a role in explaining relative merchandise sales (or are controlled by the DID estimation), then the unrestricted matching estimates are preferable since unrestricted matching allows treatment

14 observations to be paired with control observations deemed most similar. 6 Although not discussed previously, in Tables 2 and 3 the null of no time effects is never rejected, which is not a surprise since the dependent variable is annual rankings and therefore does not have a trend over time. Consequently, the unrestricted matching estimate is preferred. This, then, begs a second question: What accounts for the significant result in column 1 compared with the previous estimates? Recall, there are four main differences between the DID matching estimator and the previous estimators: (i) reliance on fewer parametric assumptions than the parametric estimators, (ii) use of only a sub-sample of the control group, (iii) relaxation of the linearity assumption, and (iv) estimation of the average treatment effect on the treated as opposed to the average treatment effect. We can partially test the relevance of (ii) by reestimating the parametric specification in column 1 of Table 2 on the matched sample used in Table 4. 7 The coefficient remains statistically insignificant. However, since the DID matching estimator uses information on lagged merchandise sales ranking, this perhaps remains an unfair comparison. Thus, we also re-estimate the specification in column 1 of Table 2 on the matched sub-sample using the change in merchandise sales ranking as the dependent variable. However, the coefficient again remains statistically insignificant. We can test the role played by (iii) be re-estimating all the models in Tables 2 and 3 using the entire sample and including the full set of interactions between all the control variables (except the logo change dummy). 8 In general, the coefficients become more positive, but remain statistically insignificant. The lone exception is the specification in column 1 of Table 3, where the coefficient on logo change doubles to 0.24 and is statistically significant at the 90% 6 This is reflected in the fact that the difference in propensity scores across matched pairs is 50% smaller on average using the unrestricted matching. 7 Note, we cannot estimate the fixed effects, AR(1), or Arellano and Bond (1991) models using the matched subsample since lagged observations are not part of the matched data, and most franchises only appear once.

15 confidence level (p = 0.08). 9 However, since the remaining three dynamic fixed effects specifications fail to find a statistically significant logo effect despite the inclusion of the full set of interactions, we conclude that controlling for lagged franchise success variables is crucial for assessing the logo effect. Once these are controlled, and they are not explicitly conditioned on in the matching framework, the basic conclusion that logo changes do not alter relative firm sales remains. Finally, we note that in principal matching methods can be used to estimate the average treatment effect (as opposed to the average treatment effect on the treated) to assess the role of (iv). This is done by re-defining non-logo changers as the treatment group and logo changers as the control group and estimating the average treatment effect on the non-treated. The matching estimate of the average treatment effect is then given by the weighted average of the average treatment effects on the treated and non-treated, where the weights are the sample proportions of the treated and non-treated (see, e.g., Persson and Tabellini, 2002). However, the disproportionate number of non-logo changers in the data (296 versus 14) makes the matching estimate of the average treatment effect on the non-treated highly suspect since the pool of potential matches for the non-treated is so small. 4. Concluding Remarks In the current business landscape, where the development and protection of copyrights is quite costly, one would expect copyrights to have a beneficial impact for firms. However, previous research in Slottje et al. (2002) fails to find a robust, positive impact of copyrights on total firm value and the demand for firm output. This study extends this work and examines the impact of copyrights in this case, logos in the National Football League on relative merchandise sales, as 8 There are 45 interactions, although not are identified and are consequently dropped from the actual estimation. In addition, the non-matching estimators still require the assumption of an additive error term.

16 a priori one would expect merchandise sales to be the most affected by logos. Using several parametric estimators, the Arellano and Bond (1991) dynamic panel estimator, and the seminonparametric propensity score matching estimator, the preponderance of the evidence suggests a statistically insignificant effect of logo changes on the relative firm sales. Due to the perhaps surprising nature of this finding, future research on the value of copyrights to firms is clearly warranted. 9 The results in this discussion are not presented in the interest of brevity, but are available upon request.

17 References Arellano, M. and Bond, S. (1991). Some tests of specification for panel data: monte carlo evidence and an application to employment equations. Review of Economic Studies 58, Blundell, R. and Costa-Dias, M. (2002). Alternative approaches to evaluation in empirical microeconomics. Portuguese Economic Journal 1, Bond, S. (2002). Dynamic panel data models: a guide to micro data methods and practice. Portuguese Economic Journal 1, Bratberg, E., Grasdal, A., and Risa, A.E. (2002). Evaluating social policy by experimental and nonexperimental methods. Scandanavian Journal of Economics 104, Cochran, W. and Rubin, D. (1973). Controlling bias in observational studies. Sankyha 35, Curry, P.A. (1998). Copyright, copy protection and feist. Research Report 9808, The University of Western Ontario. Dehejia, R.H. and Wahba, S. (1999). Casual effects in nonexperimental studies: reevaluating the evaluation of training programs. Journal of the American Statistical Association 94, Dehejia, R.H. and Wahba, S. (2002). Propensity score matching for nonexperimental causal studies. Review of Economics and Statistics 84, Eichler, M. and Lechner, M. (2002). An evaluation of public employment programmes in the east german state of sachsen-anhalt. Labour Economics 9, Ham, J.C., Li, X., and Reagan, P.B. (2001). Matching and selection estimates of the effect of migration on wages for young men. Unpublished manuscript, Ohio State Universty Department of Economics. Heckman, J.J., Ichimura, H., and Todd, P.E. (1997). Matching as an econometric evaluation estimator: evidence from evaluating a job training program. Review of Economic Studies 64, Jaffe, A. (2000). The U.S. patent system in transition: policy innovation and the innovation process. Research Policy 29, Lanjouw, J.O., Pakes, A., and Putnam, J. (1998). How to count patents and value intellectual property: uses of patent renewal and application data. Journal of Industrial Economics 46,

18 Lanjouw, J.O. (1998). Patent protection in the shadow of infringement: simulation estimations of patent value. Review of Economic Studies 65, List, J.A., Millimet, D.L., Fredriksson, P.G., and McHone, W.W. (2003). Effects of environmental regulations on manufacturing plant births: evidence from a propensity score matching estimator. Review of Economics and Statistics, forthcoming. List, J.A., Millimet, D.L., and McHone, W.W. (2002). Effects of air quality regulation on the destination choice of relocating firms. Oxford Economic Papers, forthcoming Pakes, A. (1985). On patents, r & d, and the stock market rate of return. Journal of Political Economy 93, Pakes, A. (1986). Patents as options: some estimates of the value of holding European patent stocks. Econometrica 54, Pakes, A. and Simpson, M. (1989). The analysis of patent renewal data. Brookings Papers on Economic Activity, Microeconomic Annual 1989, Persson, T. and Tabellini, G. (2002). Do constitutions cause large governments? quasiexperimental evidence. European Economic Review 46, Rosenbaum, P. and Rubin, D. (1983). The central role of the propensity score in observational studies for causal effects. Biometrika 70, Schankerman, M. and Pakes, A. (1986). Estimates of the value of patent rights in European countries during the post-1950 period. The Economic Journal 96, Slottje, D., Millimet, D.L., and Buchanan, M. (2002). Econometric analysis of copyrights. Journal of Econometrics, forthcoming. Smith, J. and Todd, P.E. (2000). Does matching address lalonde's critique of nonexperimental estimators. Journal of Econometrics, forthcoming.

19 Table 1 Summary Statistics, Variable Logo Logo Changers Non-Changers Mean Std Dev. Mean Std. Dev. Merchandise Sales Rank [p=0.19] Franchise Age (Years) [p=0.64] New Team (1 = Yes) [p=0.63] Relocated Team (1 = Yes) [p=0.76] Wins (Per Season) [p=0.01] Losses (Per Season) [p=0.01] Super Bowl Champ (1 = Yes) [p=0.40] Super Bowl Loser (1 = Yes) [p=0.00] Stadium Capacity (10,000s) [p=0.38] Population (Millions) [p=0.20] Per Capita Income (10,000s US$) [p=0.01] Unemployment Rate [p=0.09] Observations NOTE: P-values from t-tests of no difference in the means across logo changers and non-changers given in brackets.

20 Figure 1 Merchandise Sales Rankings, Select Franchises, Arizona Cardinals Dallas Cowboys New York Giants Oakland/LA Raiders Tampa Bay Buccaneers Season NOTE: Ranking measured on y-axis, where a higher ranking corresponds with greater merchandise sales (i.e., 1 = lowest, highest depends on the number of teams in the NFL in a particular season (31 in 2000)).

21 Table 2 Parametric Estimates of the Logo Effect. Independent Pooled OLS GLS-AR(1) OLS-FE OLS-FE-AR(1) Variable (1) (2) (3) (4) Logo Change (1 = Yes) (0.19) (0.14) (0.15) (0.11) Franchise Age 4.61E E * 0.11 (5.58E-03) (3.02E-03) (3.95E-03) (0.07) Victories 0.14* 0.05* 0.07* 0.01 (0.02) (0.01) (0.02) (0.01) Super Bowl Winner 0.68* 0.49* 0.43* 0.39* (1 = Yes) (0.25) (0.18) (0.19) (0.14) Super Bowl Loser * 0.32* (1 = Yes) (0.21) (0.18) (0.17) (0.14) Stadium Capacity -3.78E (10,000s) (0.01) (0.07) (0.20) (0.10) Population * (millions) (0.04) (0.02) (0.03) (0.04) Per Capita Income 0.80* 0.75* (10,000s) (0.40) (0.22) (0.43) (0.38) Unemployment Rate (0.10) (0.05) (0.09) (0.07) New Franchise * 0.49* 0.21 (1 = Yes) (0.50) (0.24) (0.25) (0.23) Relocated Franchise 0.41** (1 = Yes) (0.24) (0.37) (0.18) (0.33) Franchise Effects No No Yes Yes NOTES: Each specification includes year dummies. Standard errors in parentheses; standard errors in models in columns (1) and (3) are robust to arbitrary heteroskedasticity and correlation within franchises. * indicates significant at 5% level; ** indicates significant at 10% level.

22 Table 3 GMM Estimates of the Logo Effect (select coefficients). Independent (1) (2) (3) (4) Variable Logo Change (1 = Yes) (0.12) (0.11) (0.11) (0.11) Lagged 0.55* 0.33* 0.33** 0.29 Merchandise Ranking (0.13) (0.16) (0.20) (0.21) Twice-Lagged 0.04 Merchandise Ranking (0.06) Lagged No Yes Yes Yes Success Variables Twice-Lagged No No Yes Yes Success Variables Franchise Yes Yes Yes Yes Effects Sargan χ 2 (35)=14.18 χ 2 (35)=9.21 χ 2 (34)=6.28 χ 2 (33)=6.01 Overidentification (p=1.00) (p=1.00) (p=1.00) (p=1.00) Test H o : No p = 0.35 p = 0.96 p = 0.56 p = 1.00 autocorrelation NOTES: Each specification also includes year dummies and controls for: number of wins, whether the team won the league championship, whether the team lost in the league championship, stadium capacity, and the population, unemployment rate, and mean per capita income of the franchise's home metropolitan area. "Success variables" include wins and dummy variables indicating that the team either won the league championship or lost in the league championship. Robust standard errors or p-values in parentheses. * indicates significant at 5% level; ** indicates significant at 10% level.

23 Table 4 Propensity Score Matching Estimates of the Logo Effect. Independent Matching Algorithm Variable Unrestricted Within-Year (1) (2) Propensity Score (p=0.54) (p=0.22) Transformed Sales Ranking (τ TT, ) (p=0.13) (p=0.49) Lagged Transformed Sales Ranking (p=0.88) (p=0.74) Transformed Sales Ranking (τ DID, ) (p=0.06) (p=0.12) Wins (p=0.66) (p=0.63) Super Bowl Champion (1 = Yes) (p=0.33) (p=1.00) Super Bowl Loser (p=1.00) (p=0.30) Population (millions) (p=0.67) (p=0.67) Unemployment Rate (0 100) (p=0.52) (p=0.15) Per Capita Income (1000s) (p=0.72) (p=0.74) Franchise Age (years) (p=0.40) (p=0.38) Stadium Capacity (1000s) (p=0.80) (p=0.61)

24 Table 4 (cont.) Propensity Score Matching Estimates of the Logo Effect. Independent Matching Algorithm Variable Unrestricted Within-Year (1) (2) AFC East (1 = Yes) (p=0.06) (p=0.68) AFC Central (1 = Yes) (p=0.30) (p=0.64) AFC West (1 = Yes) (p=1.00) (p=0.56) NFC East (1 = Yes) (p=0.56) (p=0.64) NFC Central (1 = Yes) (p=1.00) (p=1.00) NFC West (1 = Yes) (p=0.30) (p=1.00) Hotelling T 2 F(14,13) = 0.38 F(14,13) = 0.34 (p = 0.96) (p = 0.97) Number of Matched Pairs Number of Unique Controls NOTES: Parameter estimates refer to the mean difference between the matched treatment and control group, where observations in the control group are weighted by the number of times they appear. P-values are associated with the null that the means are equal across the treatment and control groups. "Unique controls" reports the number of controls that are matched with at least one treatment observation.