California's exports and the 2004 overseas office closures.

Cassey, Andrew J.

I. INTRODUCTION

Nearly all states in the United States fund export promotion programs such as overseas offices. State officials often justify using tax dollars on overseas offices by claiming that the offices help small- and medium-sized firms initiate or increase exports. If overseas offices work as justified, then the state's aggregate exports to countries with an overseas office will be greater than if the offices did not exist.

Despite the general willingness of state governments to fund overseas offices--40 states had at least one in 2002--their effectiveness is unknown (although debated). Measuring the success of an overseas office is difficult because of a causality problem. If states that are good exporters use overseas offices because they are already good exporters, then the ordinary least squares regression estimate on the impact of the offices is upwardly biased. This bias potentially causes false positives on their statistical significance.

Early twenty-first-century California provides a work-around to the causality problem. California operated 12 overseas trade offices at an annual cost of $6 million. It closed all of its offices on January 1, 2004, primarily because of a 2003 state budgetary shortfall of $40 billion that forced reductions in many state programs. The budget of the entire economic development agency housing the overseas offices was eliminated. Furthermore, there was a perception that the overseas offices were ineffective after a May 2003 expose by Kindy (2003a,b) reported a lack of oversight and false claims by the offices. Although no citations for wrongdoing were issued, this expose damaged the public reputation of the offices. As of this writing, none of the offices have re-opened.

The closure of California's 12 offices provides an opportunity for a direct estimate of their impact on California's exports because the decision to close the offices was as a result of the 2003 budget crisis, an exogenous intervention. This exogenous intervention allows for an unbiased test to determine if the difference in exports from California to the set of countries with trade offices is equal to the difference in exports to a set of countries without an overseas office, before and after the January 1, 2004, closures. If there is no statistically significant difference in exports before and after the office closures compared to those where no office existed, then it cannot be the case that the overseas offices made an impact on state exports distinguishable from random events. This differences-in-differences methodology is standard. It is the unique circumstance of the California budget crisis that is key because of its exogeneity to the office-export relationship.

Applying the differences-in-differences estimator to a sample of 44 countries (12 with overseas offices) over 8 years yields a point estimate suggesting if the offices had not closed, California's exports to those countries would have been 2%-3% larger in the best case scenario. This estimate, although economically reasonable, is not statistically different from zero. Under a battery of alternative specifications and robustness checks, there is no statistically relevant impact of overseas offices on California's exports to those countries.

During the 1980s and early 1990s, international business and marketing scholars studied the effectiveness of export promotion programs, including overseas offices. The resulting literature, largely based on surveys and interviews with export promotion participants, does not reach a consensus. Wilkinson and Brouthers (2000) provide a succinct review of these early studies in addition to their own mixed findings using data from 1990.

More recently, Wilkinson, Keillor, and d'Amico (2005) examined a cross section of U.S. state export program expenditures and manufacturing exports. They find a positive correlation, but they do not control for state or country features. Cassey (2009) adapts a sales office location model to estimate how state exports to a particular country affect the probability a state would choose to facilitate that relationship with an overseas office. He estimates the value of exports an office would have to generate to be profitable. This result is conceptually different from determining the impact of existing offices. Lederman, Olarreaga, and Payton (2010) find that domestically located export promotion agencies have a statistically significant impact on country exports, but they are silent on overseas offices.

The papers by Nitsch (2007), Head and Ries (2010), and Cassey (2007) are the most similar to this paper in terms of methodology. Instead of overseas offices, these three papers study trade missions. Nitsch (2007) finds evidence for, whereas Head and Ries (2010) and Cassey (2007) find evidence against, the impact of trade missions on aggregate exports. Aware of the endogeneity problem, they control for unobserved heterogeneity using fixed effects.

Despite their best attempts, there is not enough information in the data to fully control for the bilateral unobserved heterogeneity that is the source of the bias. Head and Ries (2010) and Cassey (2007) do not have the kind of exogenous intervention provided by California's office closures. This is why they are unable to control fully for bias. Nitsch (2007) tries to control for the simultaneity bias by using the growth of exports as a regressand.

II. A HISTORY AND DESCRIPTION OF CALIFORNIA'S OVERSEAS OFFICES

California's overseas offices were trade advocacy programs physically located in a foreign country, but paid for with public monies. (1) California operated overseas offices beginning in the 1980s. The stated purpose of these offices was to promote exports, in particular the exports of small- and medium-sized firms. The offices attempted to achieve this purpose primarily by directly connecting a potential Californian exporter to foreign customers.

With the addition of an overseas office in Shanghai, China, in 2000, California operated 12 overseas offices. Along with Shanghai, the offices were located in Buenos Aires, Frankfurt, Hong Kong, Jerusalem, Johannesburg, London, Mexico City, Seoul, Singapore, Taipei, and Tokyo. In 2003, the annual budget for the 12 offices was $6 million.

Each office provided similar services. A California resident or business owner could have either contacted the overseas office directly or through an in-state office to receive export assistance. Suppose a firm in California wanted to sell merchandise in Mexico. The firm could call the Mexico City overseas office. The office would provide contacts of Mexican firms or markets likely interested in the good. These services were free of charge. Because the offices were not mandated to look for foreign direct investment opportunities, their benefits, if any, were due exclusively to increased exports.

Although all of the offices provided similar services, operational organization across the 12 offices differed. For example, state employees working abroad staffed 7 of the 12 offices, but California contracted foreign nationals in the other 5. Additionally, budgets and the number of staff differed substantially. The Mexico City office had a staff of eight and a $786,000 budget in 2003, about 60% more than the average.

The overseas offices, administered as part of the Technology, Trade, and Commerce Agency, were required by law to provide feedback on their performance. Each office evaluated its performance by asking every firm it serviced how much of their projected sales were to the foreign market. The questionnaire did not distinguish how much of this revenue was thought to be because of the services of the overseas office. After a year, the office conducted a follow-up survey in which the firm was asked if the overseas office was helpful or not. Typically the office made little effort to distinguish how much the office was helpful, or if the projected exports were realized or not. Among other problems with this method of evaluation, such as forecasting error, the survey was not objective because the jobs of the people writing the evaluations depended on the success of the office. Therefore, the reported impacts of the overseas offices were not credible. Importantly for the estimation in Section IV, this method of evaluation means that California's decision to have an office or not did not depend on current performance, but on past performance.

California experienced an economically and politically tumultuous summer in 2003. The dot-com bust dramatically reduced California's tax revenue while it was still recovering from the electricity shortage in 2002. The governor, Gray Davis, faced the possibility of a recall election. In this environment, the state legislature made the decision to close all 12 overseas offices effective January 1, 2004, as part of AB 1757. The legislature debated the bill in July 2003 and it was sent to the Secretary of State for filing on August 11, 2003. In addition to the overseas offices, AB 1757 closed the economic development agency responsible for the overseas offices. The Technology, Trade, and Commerce Agency's scope was broader than export promotion programs, lt provided grants and subsidies to promote innovation and investment in California, and small business loans.

Despite Kindy's articles asserting exaggerated success, Kress, Miller, and Koehler (2005) find the reason that the overseas offices closed was the budget crisis. Therefore, the relatively sudden closing of all overseas offices is an exogenous intervention. Supporting this claim is the fact that all offices were summarily closed rather than just those reported as most corrupt, the size of their budgets, or their location. Furthermore, the entire economic development agency was closed. Finally, because of budget crises, many states reduced their overseas office budgets during 2002-2004.

California only closed the 12 publicly funded overseas offices, lt did not close one overseas office funded privately. While the budget crisis unfolded, and the fate of the other 12 offices debated, California passed legislation authorizing an overseas office in Armenia. The legislation stipulated this office was to be solely funded with private donations. The state's only involvement was to endorse the office.

Opened in 2005, the Armenian office remains funded by private donations largely from California's Armenian community. Because this office is privately funded, it is fundamentally different than California's other offices, and therefore is not included in this study. Likewise, there are as many as nine privately funded unofficial offices that are not included in this study, either. Also, California did not close its five overseas tourism offices. Because these offices are responsible for encouraging foreign visitors to travel to California, I do not consider them overseas offices either.

III. EXPORT, OFFICE, AND OTHER DATA

The key dependent variable is exports from California to 44 countries for the years 20002007.

The year 2000 corresponds to the opening of California's newest office. The sample period includes the 4 years preceding and following the offices' closure. The before years are 2000-2003; the after years are 2004-2007.

The 44 countries in the sample are the largest in terms of importing from California over this time, accounting for 97.4% of California's exports. All 12 countries hosting an overseas office are in the sample, although Armenia is not. California exports a positive amount to all countries in the sample for all time periods. In addition to export data, I have data on real gross domestic product (RGDP) for all countries and years, and the distance from California to each country. Appendix B describes the collection and sources of the data.

Table 1 presents the summary statistics for real manufacturing exports, RGDP, and distance. I partition the data into two groups: control and treatment. The treatment group is the 12 countries that had an overseas office, and the control group is the 32 countries that did not have an office, during those 8 years. Regardless of group, there are four observations for each country before 2004 when the offices closed. These observations have been classified here as the before period and the four observations per country after the office closed as the after period. Therefore the summary statistics are across countries and 4 years of time (32x4= 128; 12x4=48).

Table 1 shows mean and median exports increased in the control group from the before to the after period. The mean in the treatment group decreased but the median did not. The difference in mean exports between control and treatment countries before and after the offices closed is $63 million. During the same time, the RGDP of both the control and the treatment groups increased in absolute terms. In relative terms, the control group grew 46% and the treatment group grew 18%. Not shown in Table 1 is that California's gross domestic product grew roughly 15% between the before and after periods.

The partition of countries into treatment and control groups is not random. California deliberately opened offices in those countries making up the treatment group. As Table 1 shows, the countries in the treatment group are much larger than the control group. Of the top five economies in the before period, California had an office in four. (It did not have an office in France.) The treatment countries are also the largest destinations for California's exports. Of California's top ten export destinations during the sample period, only Canada (third) did not have an office.

[FIGURE 1 OMITTED]

Figure 1 shows the time series of California's exports to treatment countries and control countries adjusted so that the exports to each group equals 100 in 2004. The vertical line indicates January 2004 when the offices closed. In the 4 years before the offices closed, exports to treatment and control countries track each other. Starting in 2004, the time series diverge. Exports to countries that never had an office increase, whereas exports to countries where an office closed remain flat. Note that although the outpacing of control countries' exports compared to treatment countries is likely because of the quicker relative growth of the control countries, the treatment countries grew by 18% despite the constancy of their exports.

The evidence from Table 1 and Figure 1 is enough to warrant a deeper investigation to determine the extent that closing the trade offices affected exports.

IV. ESTIMATION AND RESULTS

This section gives the results from testing if exports to treatment countries decrease compared to control countries. The test is an i-test on the means of the percent differences of exports before and after the closure between the set of countries with an overseas office and the set of countries without an office. This t-test is conceptually similar to the differences-in-differences estimator except for the other independent variables. Therefore this test cannot determine if the reason why there is a difference is because the offices closed. Thus, this t-test is a necessary, but not sufficient, condition for offices having an impact on exports.

Table 2 shows the results. Note the difference in means between the control countries and the treatment countries is 30.41. Also note the sizable difference in the standard deviations. Because of this, the t-test employed here is modified for use with unequal variances, resulting in t = 2.16 with approximately 42 degrees of freedom. Thus, there is a statistically significant difference in means with 95% confidence. The percent differences given in Table 2 are used here because the treatment countries are among the largest in the world, and thus small changes in percentage terms would be huge changes in the control group.

Because there is evidence of different outcomes for the control and treatment groups, a more sophisticated test that controls for RGDP and other independent variables is needed to estimate the impact from California's closure of 12 offices on its exports to those countries. One relationship between market size, policy variables, constant bilateral characteristics, and exports is known as the gravity equation. Introduced by Tinbergen (1962), it is widely used as an empirical international trade tool because of its simplicity, the ease in fulfilling the data requirements, and its empirical success with trade flows.

The equation is as follows:

(1) [MATHEMATICAL EXPRESSION NOT REPRODUCIBLE IN ASCII]

The real annual manufacturing export value from California to destination c in year t is denoted by [X.sub.ct]. Likewise, [Y.sub.ct] denotes RGDP. Because California is the source of the exports for all observations, its RGDP does not vary across destinations, and so it is dropped from the standard gravity equation. The treatment variable is a binary Oct which takes the value of one if California has an overseas office in country c in year t, and zero otherwise. The binary variables, [C.sub.j], capture observed and unobserved time-invariant characteristics of countries causing California to export to them. These characteristics include distance, short-term immigration demographics, and common language. These country-fixed effects also account for unobservables causing California to put overseas offices in some countries and not others. Therefore [C.sub.j] may be thought of as group effects with each of 44 groups having eight observations. The binary variables, [T.sub.k], capture California's RGDP and other time-varying variables in each year. Taking logs of both sides linearizes the gravity equation and helps with heteroskedasticity. Because there are no observations with zero exports in the sample, no observations are lost from log-linearizing.

As in Baier and Bergstrand (2007), who test the effect of free trade agreements, the gravity equation applied to panel data allows for a test of the effect of an overseas office on exports. One problem with estimating Equation (1) is the potential simultaneity of the treatment variable with exports. If there is simultaneity, the treatment variable correlates with the error term [[epsilon].sub.ct] leading to biased and inconsistent estimates. I use a natural experiment as a work-around for the simultaneity problem. Using a sample of years where no offices were introduced, the fact that California's evaluation system for the offices was recursive and not contemporaneous, and the fact that California closed the offices for reasons other than export performance convey there is no simultaneity problem between the policy and dependent variables. Therefore Oct is strictly exogenous; there is no need for instruments. In addition to this informal argument, a formal test for the strict exogeneity of the treatment variable is performed in Section V.

The time series information in the panel is used to estimate [[beta].sub.2], the coefficient of the office binary variable, using Equation (1). (2) Because both the independent and dependent variables in Equation (1) are logged, the interpretation of the point estimate for the continuous variables is the percent change in California's exports to country c in year t given a 1% change in the independent variable. The interpretation of the coefficient on the binary variables is the exponentiation of the coefficient minus one, or approximately the percent change in exports because of a switch from zero to one in the binary variable divided by 100. Because the treatment variable is one in the before years for the treatment group and zero in the after years for both groups, the coefficient on Oct is the estimated percent change (divided by 100) in [X.sub.ct] if the treatment is not performed. In other words, it is the percent change (divided by 100) in exports if the offices were not closed but remained open. Although it is unlikely, there is a possibility that the overseas offices were ineffective to the point that they decreased exports compared to if they were not open. This could occur if the overseas offices matched exporters with inept importers. Therefore a two-sided test is used.

Diagnostic tests indicate that some adjustments are in order. A Breusch-Pagan test rejects the null of homoskedasticity ([chi square](1)= 35.71). In addition, the Wooldridge (2002, 177) test rejects no first-order autocorrelation (F(1,43) = 12.841). Therefore, as recommended by Bertrand, Duflo, and Mullainathan (2004), I use standard errors clustered at the country level (not country-year clusters per their recommendation). These standard errors, indicated in Table 3 with brackets, are robust to heteroskedasticity and country-level serial correlation.

Table 3 shows the results. Observations are weighted by their RGDP, putting more emphasis on the bigger countries in the sample to de-emphasize noise created by extremely small exports to small countries. The goodness of fit improves slightly and the root mean square error (RMSE) drops compared to the unweighted model, but none of the results depend on this weighting design. The coefficient on the treatment dummy indicates keeping the offices open would have increased exports to each of those countries by slightly less than 1.2% on average. Although this estimate is economically significant and plausible, it is not statistically significant, indicating the overseas offices did not statistically increase state exports.

One potential problem in measuring the impact of the overseas offices on exports is the time delay of closing them. It seems unlikely that established trade relationships die immediately when an overseas office closes. The more plausible case is that trade relationships end after a year or two, as described in Besedeg and Prusa (2006), and that closing the offices prevents some new exports from occurring. This would result in a decrease in exports compared to the case that the offices remained open in years following 2004. Thus Equation (1) is estimated using a series of lagged treatment variables, [O.sub.c,t-1], [O.sub.c,t-2], and [O.sub.c,t-3]. The results are given in Table 3. Again observations are weighted by RGDP and standard errors are clustered at the country level. And as before, the estimates for the treatment variables are economically significant and plausible but not statistically significant. The coefficient on the cumulative office variable is the sum of the individual lag coefficients whether they are individually statistically significant or not. It is the average impact of offices after 4 years. The F-statistic from testing the joint hypothesis that all of the coefficients on the treatment and lagged treatment variables are zero is never statistically significant.

As an alternative to estimating Equation (1), first differences are taken, yielding:

(2) [MATHEMATICAL EXPRESSION NOT REPRODUCIBLE IN ASCII]

Besides eliminating potential omitted variables, the first difference estimator is more efficient than the fixed effects estimator used for Equation (1) when there is serial correlation (Wooldridge 2002, 284). There is heteroskedasticity in the first differenced errors ([chi square](1) = 16.64).

In Table 4, the coefficient [[beta].sub.1] is the increase in [X.sub.ct] / [X.sub.ct-1] because of a 1% increase in [Y.sub.ct] / [Y.sub.ct-1], and [[beta].sub.2] is the exponentiated increase (minus one) in [X.sub.ct]/ [X.sub..ct-1] as a result of not closing the offices. Differentiating Oct yields a binary variable that is one when the offices close and zero otherwise. Thus the estimates given in Table 4 are directly comparable to those in Table 3. The estimate for the impact of the overseas offices doubles from Table 3 to 2.4%. And the standard errors are smaller. Regardless of this, the estimate for the impact of the overseas offices remains not statistically significant. As before, the specifications with lagged policy variables are estimated to test if the impact of the office closures does not appear until after the fact. Again, neither the F-statistic on their joint significance nor any of the individual coefficients on lagged policy are statistically significant.

The closing of California's overseas offices is a natural experiment in which the exogenous intervention avoids the simultaneity of the treatment variable problem. Because of this exogeneity, the differences-in-differences estimator is unbiased and consistent when testing for the impact of the overseas offices on exports using the gravity equation to control for RGDP. The results from Table 4 are not different than those given in Table 3. There is no evidence that closing California's overseas offices resulted in statistically less exports to those countries than if the offices had remained open. In the next section, several robustness checks are run, beginning with a test of the exogeneity of the treatment variable.

V. ROBUSTNESS OF RESULTS

The estimate for the impact of overseas offices on California's exports is not statistically significant in any specification yet tested. In this section, the robustness of this finding as well as the formal testing for the exogeneity of the treatment variable are checked. In addition to the checks below, there are more specifications in Appendix S 1 (Supporting Information). Finally, robustness checks using fixed effects generalized least squares on Equation (1) are conducted, but the results are not reported because the estimates do not change much, and the statistical significance does not change at all.

A. Exogeneity of Treatment

The key to the consistency and lack of bias of the estimators used in Section IV is the exogeneity of the policy variable Oct. In Section II, it is argued the reason why California closed all of its overseas offices (as well as the entire Technology, Trade, and Commerce Agency) was because of a government budget deficit and not because of the performance of the offices with respect to exports. In addition, the sample period beginning in 2000 is chosen so that no office opened or closed other than for state budgetary reasons. Therefore, neither the past, present nor the future values of the policy variable is correlated with the error term; the treatment is strictly exogenous.

It is not reasonable to believe that there is contemporaneous correlation between Oct and [[epsilon].sub.ct]. As described in Section II, performance of the office was evaluated using survey results from the past year. Therefore, if there is correlation before the closures it has to be because of past values.

Following Baier and Bergstrand (2007), the correlation of office closures with past values is tested by including a leading treatment variable, [O.sub.ct+1]. This test for strict exogeneity is suggested by Wooldridge (2002, 285). The first specification given in Table 5 shows the results. The coefficient on the lead treatment term is not statistically significant. Therefore, the California office closures pass the exogenous intervention test. Another interpretation of the results in Table 5 is that the news of the trouble at the Technology, Commerce, and Trade Agency did not cause an anticipatory impact before the offices actually closed.

Next, I consolidate Equation (2) down to two periods, before and after the closures, by averaging exports and RGDP by country across time. The treatment binary variable is one for those countries with an office in the before period and otherwise zero. Therefore it is not possible for [O.sub.cB] to correlate with [[epsilon].sub.cB] (where B indicates the before period) because California's evaluation procedure for the offices relied on past performance. Because there is no past performance in this case, there can be no correlation between past exports and the treatment variable. In addition, reducing to two periods eliminates the serial correlation problem addressed by Bertrand, Duflo, and Mullainathan (2004). And thus this test serves as a robustness check on our use of standard errors clustered at the country level. After the reduction to two periods, the logged independent variables are differenced yielding 44 observations. The drawback of this method is the decrease in observations from losing the full time series yields a test with lower power.

The results are shown in the second row of Table 5. Again the estimated coefficient on office is not statistically significant. The estimates given in Table 5 support the strict exogeneity of [O.sub.ct] assumption.

RGDP is assumed to be exogenous although exports are a part of RGDP. This is because net exports are part of RGDP, not gross exports, and the percent of net exports to RGDP is small in most countries. See Baier and Bergstrand (2007) for more on the exogeneity of RGDP in the gravity equation. Using the same tests as before, I find RGDP is exogenous also.

B. Controlling for Changes in the Treatment Countries

There is a possibility the import propensity of the treatment countries decreased for reasons outside the gravity equation. This would underestimate the impact of the overseas offices. A look at the data does not give an indication that this occurred. Exports from other U.S. states increased 15% to the treatment countries, showing that the propensity of the treatment countries to import from the United States did not fall.

To test for this possibility formally, the size of the sample is increased to include 42 U.S. states that exported a positive amount each year to the 44 countries in the sample. (3) I add data on RGDP by state and data on distance from the population centroid of each state to the capital of each country. Increasing the sample allows for country-year fixed effects to control for import propensity as measured against imports from states other than California. Therefore it is estimated as:

[MATHEMATICAL EXPRESSION NOT REPRODUCIBLE IN ASCII]

where [S.sub.t] are state fixed effects (N = 14784, [R.sup.2] = .99, RMSE = .61). The policy variable [O.sub.sct] includes the closing of California's offices as well as the office locations of all states in 2002. As usual, RGDP weights and standard errors clustered at the country level are used. Double stars indicate statistical significance at the 5% level.

Because the fixed effects do not control for all possible missing variables (such as time invariant state-country variables affecting exports besides distance), first differences are taken and estimated again. The estimated coefficient on the differenced office variable is -.500 [.0475] and is not statistically significant at the 10% level. Therefore expanding the sample to include other U.S. states and control for treatment countries over times does not change the lack of evidence that the overseas offices impacted exports statistically.

C. Measurement Error in the Treatment Variable

A final potential problem is that there may be systematic measurement error in the treatment binary that creates correlation with the error term in Equation (1). The treatment binary [O.sub.ct] treats all offices equally although they differed in their budget and the type of employees. The Mexico office had a budget five times greater than the Singapore office. Also the offices in South Korea, China, Singapore, Argentina, and Israel were contracted, whereas the other seven offices were operated by California. Therefore, I run two alternative specifications. First, I replace the treatment binary with a continuous variable, Office Budget, indicating the fraction of California's total expenditure on overseas offices received by each office. Second, I use two treatment binary variables: a dummy, Office CA, that is one if the office is run by Californian employees and another dummy, Office Contract, that is one if the office is run by contract employees. Results are given in Table 6.

The estimated coefficient on the treatment variable when budget shares are used increases by an order of magnitude but remains not statistically significant. The same is true when both lagged and first differenced budget variables are included (not reported). When the treatment is split into dummies for California-operated offices and contracted offices, the estimated coefficient on the contract dummy is statistically significant at the 10% level. This holds when lagged terms are included, but not when terms are first differenced. The coefficient, however, is negative indicating that closing the contract offices increased California's exports to those countries.

Although there is statistical significance on a treatment coefficient in Table 6, these results are not considered a challenge to the findings from Section IV because of its negative sign. If the ineffectiveness or counter-effectiveness is responsible for the lack of statistical significance in Section IV, then the coefficient on office CA should be statistically significant. It is not. Furthermore, office contract is only statistically significant for the fixed effects estimator and not the first differences estimator, indicating the result is not robust.

VI. CONCLUSION

A direct estimate of the impact of state export promotion programs on state exports is difficult to obtain because the program variable might be correlated with the error term, an endogeneity problem. Ignoring this problem leads to biased and inconsistent estimates. The California budget crisis of 2003 is an exogenous intervention because it was the budget crisis, rather than export performance, that caused the demise of all 12 of California's overseas offices. In this case, the differences-in-differences estimator gives unbiased and consistent estimates of the impact of the closures on state exports to those countries.

I apply both fixed effects and first differences in a differences-in-differences estimator to a gravity equation to estimate the impact the closure of the overseas offices has on California's manufacturing exports. Although the estimates differ from specification to specification, they range up to an average increase in the exports of 2%-3% per year. These estimates are not statistically significant. Therefore, there is no statistical evidence that closing California's offices was detrimental to California's exports. This brings into doubt the effectiveness of overseas offices, and of state export programs more generally, all over the United States.

ABBREVIATIONS

GDP: Gross Domestic Product

N: Number of observations

RGDP: Real Gross Domestic Product

RMSE: Root Mean Square Error

APPENDIX A

Newspaper Articles and Government Documents Referenced

The details of California's overseas offices, and of their closing, come from various newspaper articles and California state government documents. Much of the information in these publications overlaps. Rather than choosing one or two to list as a parenthetic citation in the text for each new piece of information, those that have been consulted are listed.

Access World News. "State to Close Trade Offices Worldwide by Year-end," 7 August 2003.

Armstrong, D. "Trade Offices Could Close--Victims of State Budget Cuts," The San Francisco Chronicle, 29 July 2003.

Associated Press. "Davis Signs Bill for Armenian Trade Office if State Can Get Funds," 25 September 2002.

--. "State Senators to Probe Reported Fraud by Cal Trade Offices," 1 June 2003.

Business Wire. "California Foreign Office Directors Visit Bay Area," 10 May 2001.

Chan, G. "California is Close to Losing its Chief Economic Development Agency," Sacramento Bee, 29 July 2003.

Department of Finance. "State of California Final Budget Summary 2002-03." State of California, n.d. Accessed June 15, 2009. www.documents.dgs.ca.gov/ osp/GovernorsBudget/pdf/2002-03budsum.pdf

--. "Technology, Trade, and Commerce Agency." State of California, n.d. Accessed September 10, 2008. www.dof.ca.gov/HTML/Budget_05-06/Budget/2900.pdf

Joseph, B. "Foreign Trade Offices Could Make a Comeback," The Orange Country Register, 29 April 2006.

Legislative Analyst's Office. "Analysis of the 2001-02 Budget Bill, Technology, Trade, and Commerce Agency (2920)." State of California, n.d.

--. "Analysis of the 2003-04 Budget Bill, Technology, Trade, and Commerce Agency (2920)." State of California, n.d.

Los Angeles Times. "State's Solo Trade Office Facilitates Few Deals," 30 July 2007.

Schneider, A.C. "Slow Recovery for State Export Promotion," The Kiplinger Letter, 5 January 2006.

APPENDIX B

Data Description and Sources

Data on California's manufacturing exports are from the Origin of Movement data series collected by the U.S. Census and released through the World Institute for Strategic Economic Research (2005). These data are recorded at the port of exit by collecting an export declaration form (or electronic equivalent) in which questions ask the state of origin and destination of the shipment. Two issues potentially affect the quality of the data. The first is that the export value includes inland transportation and insurance costs, thus making the value of an interior state's exports greater than the equivalent border state's exports. The second is that the data are the state of origin of the outbound shipment or the state of shipment consolidation rather than the state of production. In addition to a detailed description of this data, Cassey (2009b) performs a variety of diagnostic tests. He finds consolidation for mining and agricultural exports is a severe problem, but not a serious problem for manufacturing exports. Furthermore, the extent that California's reported exports are actually from Californian firms is not relevant for this study because differences-in-differences will not be affected unless there is a change in inland transportation or consolidation corresponding to the year the offices closed.

The source of the office location data is a survey conducted by the Council of State Governors as reported by Whatley (2003). Additional information is available from California state websites, press releases, and newspaper articles listed in Appendix A. Finally, data on GDP are from the International Monetary Fund's (2009) World Outlook Database, April 2008. The current year values for exports and GDP are converted into real values by applying the U.S. Producer Price Index (all commodities less fuel) from the U.S. Bureau of Labor Statistics (n.d.).

REFERENCES

Baier, S. L., and J. H. Bergstrand. "Do Free Trade Agreements Actually Increase Members' International Trade?" Journal of International Economics, 71(1), 2007, 72-95.

Bertrand, M., E. Duflo, and S. Mullainathan. "How Much Should We Trust Differences-in-Differences Estimates?" Quarterly Journal of Economics, 119(1), 2004, 249-75.

Besedes, T., and T. J. Prusa. "Ins, Outs, and the Duration of Trade." Canadian Journal of Economics, 39(1), 2006, 266-95.

Cassey, A. J. "Estimates on the Impact of a State Trade Mission on State Exports." Manuscript, University of Minnesota, 2007.

--. "The Location of U.S. State's Overseas Offices." 200%. School of Economic Sciences, Washington State University working paper no. 2009-10.

--. "State Export Data: Origin of Movement vs. Origin of Production." Journal of Economic and Social Measurement, 34(4), 2009b, 241-68.

Head, K., and J. Ries. "Do Trade Missions Increase Trade?" Canadian Journal of Economics, 43(3), 2010, 754-75.

International Monetary Fund. World Economic Outlook Database. Washington, DC: International Monetary Fund, 2009.

Kindy, K. "Special Investigation Trade Secrets." The Orange County Register, 25 May 2003a, Sec. News, p. Cover.

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SUPPORTING INFORMATION

Additional Supporting Information may be found in the online version of this article:

APPENDIX S1: The details of the many alternative specifications and robustness checks.

Please note: Wiley-Blackwell are not responsible for the content or functionality of any supporting materials supplied by the authors. Any queries (other than missing material) should be directed to the corresponding author for the article.

(1.) Many of the details in this section are from newspaper articles and state of California government documents whose information overlaps each other. Rather than citing all sources or each point, a list of consulted sources is given in Appendix A.

(2.) Estimating a "naive" specification of Equation (1) without the country fixed effect yields point estimates for office of 1.12 *** [.38 country cluster standard errors], where *** indicates the coefficient is significant at the 1% level.

(3.) None of the following results change if only the top ten exporting states are used.

ANDREW J. CASSEY, I thank Ron Mittelhammer and three anonymous referees for outstanding suggestions, participants at the Eastern Economic Association 2009 Meeting and Western Regional Science Association 48th Annual Meeting, and Robert Rosenman for suggesting Economic Inquiry.

Cassey: Assistant Professor, School of Economic Sciences, Washington State University, 101 Hulbert Hall, Pullman, WA 99164. Phone 1-509-335-5555, Fax 1-509-335-1173, E-mail cassey@wsu.edu

doi: 10.111 l/j.1465-7295.2010.00337.x TABLE 1 Summary Statistics of the Exports and RGDP for Group and Period variable Group Period N Mean Median Real exports Control Before 128 723.32 234.88 (millions) Control After 128 765.34 388.55 Treatment Before 48 3,443.32 2,833.78 Treatment After 48 3,422.19 2,884.19 RGDP Control Before 128 207.43 130.05 (billions) Control After 128 303.72 186.70 Treatment Before 48 664.72 281.17 Treatment After 48 784.26 337.34 Distance Control -- 128 6,033.88 5,858.50 (miles) Treatment -- 48 6,394.17 6,186.00 variable SD Min. Max. Real exports 1,310.63 42.11 8,779.07 (millions) 1,295.05 71.38 8,140.40 3,169.49 61.05 11,894.92 2,945.78 105.16 11,354.40 RGDP 236.97 8.16 1,243.69 (billions) 327.21 9.36 1,498.10 833.26 59.83 3,276.34 873.80 72.05 3,041.67 Distance 1,662.74 2,365.00 8,886.00 (miles) 2,030.32 1,656.00 10,408.00 Notes: The summary statistics are with respect to country-years. SD, standard deviation. TABLE 2 T-Test on Percent Difference in Mean Exports Before and After 2004 by Group Group N Mean SE SD Control 32 37.32 12.16 68.77 Treatment 12 6.92 7.10 24.59 Differences -- 30.41 ** 14.08 -- Notes: The date are present differences in mean exports between the years 2000-2003 and 2004-2007, from California to each of 44 destinations. Using a formula for unequal variances. t = 2.16. SD, standard deviation; SE, standard error. ** Significant at the 5% level. TABLE 3 Differences-in-Differences Estimates with Lagged Treatments N [R.sup.2] RMSE RGDP Office Lag Office 352 .99 .15 .69 *** .0116 -- [.16] [.0904] 308 .99 .14 .66 *** .0101 .0275 [.12] [.0797] [.0859] 264 .99 .13 .67 *** .0102 .0137 [.13] [.0712] [.0543] 220 .99 .12 .64 *** .0231 .0146 [.15] [.0776] [.0567] N Lag2 Office Lag3 Office Cum. Office 352 -- -- .0116 308 -- -- .0377 264 .0189 -- .0429 [.0594] 220 -.0040 .0466 .0803 [.0585] [.0450] Notes: All regressions are of log [X.sub.ct] = [alpha] + [[beta].sub.1] log [Y.sub.ct] + [[summation of].sup.44.sub.j=2] [[delta].sub.j][C.sub.j] + [[summation].sup.2007.sub.k=2001] [[delta].sub.k][T.sub.k] + [[epsilon].sub.ct] with various lags of [O.sub.ct]. The constant, country, and time dummies estimates are not reported. Standard errors [in brackets] are clustered at the country level. Observations are weighted by [RGDP.sub.ct]. *** The coefficient is significant at the 1% level. TABLE 4 Differences-in-Differences Estimates with First Differences and Lagged Treatment N [R.sup.2] RMSE RGDP Diff. Office Lag Diff. Office 308 .41 .13 .67 *** .0236 -- [.09] [.0716] 264 .41 .13 .65 *** -- .0164 [.081 [.0455] 220 .16 .24 .61 *** -- -- [.09] 264 .41 .13 .65 *** .0243 .0168 [.07] [.0708] [.0446] 220 .25 .23 .59 *** -- .0198 [.10] [.0468] 220 .26 .13 .58 *** .0268 .0204 [.09] [.0702] [.0457] N Lag2 Diff. Office Cum. Office 308 -- .0236 264 -- .0164 220 -.0037 -.0037 [.0492] 264 -- .0654 220 -.0031 .0167 [.0502] 220 -.0026 .0446 [.0493] Notes: All regressions are of the form log [X.sub.ct] - log [X.sub.ct] = [[beta].sub.1] (log [Y.sub.ct] -log [Y.sub.ct]) + [[beta].sub.2] ([O.sub.ct] - [O.sub.ct-1]) + [[summation].sup.2007.sub.j=2001] ([[delta].sub.j][T.sub.j] - [[delta].sub.j-1][T.sub.j-1]) + ([[epsilon].sub.ct] - [epsilon].sub.ct-1]) with various lags of [O.sub.ct] -[O.sub.ct-1]. The differenced time dummies estimates are not reported. Standard errors [in brackets] are clustered at the country level. Observations are weighted by [RGDP.sub.ct]. *** The coefficient is significant at the 1% level. TABLE 5 Testing the Exogeneity of the Treatment Variable Lead N [R.sup.2] RMSE RGDP Office Office After 308 .99 .14 .71 *** .0274 -.0442 -- [.21] [.0543] [.0884] 44 .38 .19 .73 *** .0070 -- -.12 [.18] [.0710] [.08] Notes: The first specification is log [X.sub.ct] = [alpha] + [[beta].sub.1] log [Y.sub.ct] + [[beta].sub.2][O.sub.ct] + [[summation].sup.44.sub.j=2] + [[summation].sup.2007.sub.k=2001] [[delta].sub.k][T.sub.k] + [[beta].sub.3] log [O.sub.ct+1] + [[epsilon].sub.ct]. The second specification is (log [X.sub.cA] - log [X.sub.cB] = [[beta].sub.1] (log [Y.sub.cA] - log [Y.sub.cB]) + [[beta].sub.2] ([O.sub.cA] - [O.sub.cB]) + [[delta].sub.A] + ([[epsilon].sub.cA] - [[epsilon].sub.cB]). Observations are weighted by [RGDP.sub.ct]. *** The coefficient is significant at the 1% level. TABLE 6 Measuring the Treatment Differently Office Office N [R.sup.2] RMSE RGDP Budget Office CA Contract 352 .99 .15 .68 *** .1629 -- -- [.131 [.4336] 352 .99 .15 .59 *** -- .0955 -.1505 * [.11] [.0669] [.0812] 308 .99 .13 .55 *** -- .0673 -.1092 * [.11] [.0752] [.0608] 308 .42 .13 .66 *** -- -- -- [.11] Lag N Diff. CA Diff. Contract Lag CA Contract 352 -- -- -- -- 352 -- -- -- -- 308 -- -- .0459 .0051 [.0969] [.0726] 308 .0457 -.0400 [.0722] [.0692] Notes: Standard errors [in brackets] are clustered at the country level. Observations are weighted by [RGDP.sub.ct] *** The coefficient is significant at the 1% level; * the coefficient is significant at the 10% level.