Economic reforms and industrial policy in a panel of Chinese cities

Abstract

We study the effect of place-based industrial policy on economic development, focusing on the establishment of Special Economic Zones (SEZ) in China. We use data from a panel of Chinese (prefecture-level) cities from 1988 to 2010. Our difference-in-difference estimation exploits the variation in the establishment of SEZ across time and space. We find that the establishment of a state-level SEZ is associated with an increase in the level of GDP of about 20 %. This finding is confirmed with alternative specifications and in a sub-sample of inland provinces, where the selection of cities to host the zones was based on administrative criteria. The main channel is a positive effect on physical capital accumulation, although SEZ also have a positive effect on total factor productivity and human capital investments. We also investigate whether there are spillover effects of SEZ on neighboring regions or cities further away. We find positive and often significant spillover effects.

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Notes

  1. 1.

    More precisely, we use data on prefecture-level cities, which are administrative units below provinces and above counties. See Sect. 3 for details.

  2. 2.

    Akinci and Crittle (2008) provide a cross-country comparison specifically focusing on different types of special economic zones and their role for development.

  3. 3.

    Wei (1993) uses two samples: the first has 434 cities but only a limited time variation from 1988 to 1990. The second sample includes fewer cities (74) and covers the period 1980–1990.

  4. 4.

    See Perkins (1988), Naughton (2007), Brandt and Rawski (2008), and Xu (2011).

  5. 5.

    For more detailed analyses of the economic growth of China before and after the start of economic reforms, see Cheremukhin et al. (2015), Song et al. (2011), and Storesletten and Zilibotti (2014).

  6. 6.

    The SEZ status implied tax deductions, special tariffs for import and export, and exemptions from the regulations on foreign exchange and land use. Foreign firms that resided inside of the SEZ first enjoyed 2 years of tax holiday, then 3 years of a low tax rate of 7.5 %, and after the initial 5 years a tax rate of 15 %. Outside of the zones, the tax rate for foreign firms was 33 % and for state-owned firms 55 % (see Wei 1993).

  7. 7.

    See Sect. 2.2 for details on the difference between the zones.

  8. 8.

    Online Appendix Table A1 lists the number of state-level and province-level development zones and their average share of industrial output in three coastal provinces hosting a large share of SEZ. The data are from WEFore (2010) for the year 2009. All three provinces have a larger number of province-level than of state-level zones (a ratio of 7:1). However, the state-level zones account for a far larger share of industrial output.

  9. 9.

    Such competition is also a concern in other countries. See for example Ossa (2015) for a general equilibrium analysis of subsidy competition in the U.S.

  10. 10.

    We complement the dataset with data from the NBS published in New China City in 50 Years Statistical Collection and the New China in 60 Years Provincial Statistical Collection, mainly to fill gaps in the China City Statistical Yearbooks. Provincial data is obtained from New China in 60 Years Statistical Collection. The source for the light data is the National Geophysical Data Center of the National Oceanic and Atmospheric Administration (NOAA). More detailed information about the data sources is provided in the online appendix and the variables are defined in Sect. 3.1.

  11. 11.

    Although we can track border changes (of the core and the periphery) over time by controlling for land area as reported in the statistical yearbooks, they are less of a concern when considering the larger area.

  12. 12.

    The digital maps were obtained from the Australian Consortium for the Asian Spatial Information and Analysis Network (ACASIAN). Note that, unlike for GDP, we can hold the area of the urban core constant when measuring light intensity based on the 2010 maps. The concerns due to border changes therefore do not apply here.

  13. 13.

    A detailed description of this process can be found in Online Appendix B.

  14. 14.

    For the dependent variable we show the statistics for real GDP based on provincial price deflators, but in the empirical analysis we use nominal GDP because the province-year fixed effects absorb price changes at the province level. See also the next section.

  15. 15.

    The real GDP index of cities is available from the NBS for the period 1996–2010. For this period, cities with a SEZ had an average yearly inflation rate of 1.8 %, while cities without a SEZ had an average of 2.3 %. The difference is not statistically significant. We also run a panel regression of prices on the reform indicator and control for city and province-year fixed effects. The estimate is \(-0.008\) and insignificant.

  16. 16.

    In an earlier version, we also show results for GDP per capita if one does not control for population. The results are qualitatively similar to those shown in Table 3.

  17. 17.

    We also construct a similar separate dummy variable for province-level reforms. Note that including the year of the reform in the dummy does not alter the baseline results significantly.

  18. 18.

    In the Sect. 7.5 we discuss the results when instead of controlling for land area we allow for structural breaks in the city fixed effects when there are border changes.

  19. 19.

    The coefficient on population size is negative, suggesting that an increase in the population size due, e.g., to immigration, has a negative effect on labor productivity.

  20. 20.

    This specification in column (3) is equivalent to controlling for the logarithm of population density and land area. In Sect. 7.5 we investigate the role of density in more detail, and we also discuss the concern that population and population density could be endogenous. The results are robust to using lagged variables and alternative ways of controlling for border changes.

  21. 21.

    In the sub-sample of inland cities, 44 cities were granted SEZ status. Of these, 18 were provincial capitals.

  22. 22.

    Arguably, inland capitals are per se a special group. Since the selection of treated cities was based on an administrative criterion (rather than on unknown, possibly heterogeneous criteria), we can better control for features making capital cities different from the control group. In Sect. 4.4 we allow cities to have year fixed effects that depend on such city characteristics, and we find that the results are similar.

  23. 23.

    We also explored longer lags. The lags for 5 years prior to the reform are never significant in the full sample. In the inland sample some of the earlier lags become significantly negative but only in the specification in column (4) that does not control for changes in land area. Note that lags longer than 3 years are identified out of a significantly smaller set of reforming cities (since many cities were granted the SEZ status in the early 1990’s, and our sample starts in 1988). For instance, in the full (inland) sample the first three lags are identified out of 75 (31) cities, while the fifth lag would only be identified out of 31 (18) cities.

  24. 24.

    Note also that the earliest zones (for example the CSEZ) introduced before 1989, likely the most selected group, are either excluded or exhibit no time-variation in the policy indicators in our sample period. Thus, they play no role in the identification of the treatment effect.

  25. 25.

    It would be possible to also include the term \(\alpha _{1}I\_Reform_{it}\) to this specification. However, it is very difficult to identify separately all the effects in such a highly parameterized model. Therefore, we omit this term, and regard the current specification as a non-nested alternative to Eq. (2).

  26. 26.

    \(\hat{\alpha }_{3}\) and \(\hat{\alpha }_{4}\) are jointly significant at 5 % in the full sample and at 10 % in the inland sample.

  27. 27.

    Clearly, the quadratic model is not a correct specification itself, since it would imply a negative long-run effect of SEZ. Given the short sample, the data only capture the increasing part of the quadratic relation. See Sect. 4.5 for a more general specification.

  28. 28.

    We calculate for each year the median of the variables across all cities. When we restrict the regression sample to inland provinces, then we calculate the difference relative to the median in this restricted sample. Since our sample is an unbalanced panel, the year in which cities appear in our sample can vary. However, the results are robust to restricting the sample to a balanced panel of 172 cities. The sample size is reduced here because of missing data for the number of universities, but the results are also robust to excluding the interactions with the initial number of universities and thus using the larger sample.

  29. 29.

    Consider for example a city i that enters our sample in 1988,  and whose GDP p.c. is reported in the yearbook. The interaction effect between a year dummy (for example 1995) and the log difference between GDP p.c. in 1988 and the median in that year then is

    $$\begin{aligned} D_{1995}\times \left[ \log (GDP_{1988,i})-\log (GDP_{1988,median})\right] . \end{aligned}$$

    The estimate on this interaction would capture how much higher GDP p.c. is in 1995 for city i when the log difference changes by some percentage. Therefore, cities with median initial characteristics have a time path as given by the main year dummies, and the interactions with initial characteristics allow differential relative paths for cities above or below the median.

  30. 30.

    The difference between Panel A and B in the sample size is due to cities with zero universities in the first year, such that the log difference in Panel A is not defined.

  31. 31.

    For the same reasons described in the discussion of Table 4, we do not include more pre-reform indicators. When we include also indicators for 4 and 5 years prior to the reform, these indicators are marginally significant, but identified by only 27 observations.

  32. 32.

    When the cities reformed in 1991 and 1992 reach the year 2010, the subsequent number of cities that identify the individual coefficients drops from 54 to 9. The vertical dashed line in the figure marks this drop.

  33. 33.

    The reforms in the inland provinces started almost a decade later than in the coastal provinces. The post-reform effects are therefore estimated for a shorter period and based on fewer observations. In separate regressions not shown here, we find that if residuals are clustered at the province\(\times \) years of reform (instead of city) level, the effects after 9 years are mostly statistically significant and positive in the inland sample. Two of the pre-reform indicators are also significant but negative.

  34. 34.

    It should be noted that the estimates on OtherTypes are based on few observations. 14 cities have a zone type other than ETDZ, HIDZ, or EPZ, but in 11 of these the zone this is in conjunction with an ETDZ or HIDZ.

  35. 35.

    The stark drop in OtherTypes is identified by only one observation. EPZ were established after 2000 and often inside an existing zone. Furthermore, the EPZ may have gained importance after the WTO accession in 2001, which could explain their upward trend (though insignificant).

  36. 36.

    Recall that some zone types like ETDZ and HIDZ may target cities with certain characteristics such as having universities. This could raise concerns about selection and we address this in a similar fashion as in Sect. 4.4. When we include the interactions of year fixed effects with initial characteristics (GDP p.c., population, density, and number of universities), then the estimates on these zone types are relatively similar. The two exceptions are that in column (5) ETDZ becomes significant while HIDZ loses significance and that in column (6) ETDZ becomes significant.

  37. 37.

    The estimation of production functions can suffer from simultaneity bias, because profit-maximizing firms choose inputs after knowing the realization of productivity shocks, and selection bias, related to exit and survival of firms. In the firm-level literature, it is common to use the correction proposed by Olley and Pakes (1996). For example, Brandt et al. (2012) find that the TFP growth of Chinese firms is underestimated when the endogeneity bias is uncontrolled for. Martin et al. (2011b) estimate a Cobb-Douglas production function using firm level data. They find that after controlling for simultaneity bias, TFP is still very close to the one obtained using a simple OLS estimation. Since we use aggregate data, we follow the traditional approach and use an OLS estimator. This is related to the growth accounting literature including Hall and Jones (1999) and Caselli (2005). See also Hsieh and Moretti (2015) for an application to city-level data.

  38. 38.

    More formally, we let

    $$\begin{aligned} \log TFP_{it}=logY_{it}-{\hat{\alpha }}\times logK_{it}-{\hat{\beta }}\times log\left( h_{it}L_{it}\right) -{\hat{\gamma }}_{pt}-{\hat{\chi }}_{i}, \end{aligned}$$
    (5)

    where \(Y_{it}\) is GDP, \(K_{it}\) is physical capital stock, \(h_{it}\) is human capital, and \(L_{it}\) is population; \(\hat{\alpha }\) and \(\hat{\beta }\) are the estimated coefficients of the Cobb-Douglas production function; \(\hat{ \gamma }_{pt}\) is the estimated province-year dummy, and \(\hat{\chi }_{i}\) is the estimated city fixed effect capturing, respectively, province-level common trends and city-level time-invariant components of productivity. \( TFP_{it}\) measures the city\(\times \)time variation in TFP.

  39. 39.

    The difference is likely due to non-hukou population which is captured in the census data but not in the yearbook data. Since in panel A we compute population for the years in between the census based on the growth rate in the yearbooks, the annual variation does not fully reflect non-hukou migrants and is subject to measurement error. See also Sect. 7.4, where we discuss the use of census data.

  40. 40.

    Ideally, we would prefer to use the educational attainment of the working population (age 25–64). However, this is not available in the census. In Appendix Table A4 we break down the result by different educational levels. The most salient effect is the increase in the share of college graduates.

  41. 41.

    The result is similar when we split the sample into a pre- and post-2000 period.

  42. 42.

    This is consistent, among others, with Rosenthal and Strange (2004). Geographic distance (or transportation costs) plays also a central role in the literature on trade and economic geography (Fujita et al. 1999). An alternative measure of distance is used by Bloom et al. (2013) who argue that cross-firm spillovers depend on the distance in technology and product markets. Neumark and Kolko (2010) also use the identification assumption that the effect of place-based policy on non-targeted areas differs in the distance to the treated areas.

  43. 43.

    Jaffe et al. (1993) find that patent citations are highly spatially clustered, which implies that there is a distance decay in the knowledge diffusion. Keller (2002) finds that the benefit of technology spillover is halved with a distance of 1200 km.

  44. 44.

    We use the tool traveltime3 in Stata that accesses the Google maps. Since only a limited number of queries can be submitted and there are more than 75’000 routes, we measured the distance of each bilateral connection in only one direction and imposed symmetry.

  45. 45.

    The tool in ArcGIS is cost distance and is an implementation of the Dijkstra algorithm. See for example Alder (2015) for a description of this method and the data.

  46. 46.

    We assume that all distance measures have a linear relationship with effective transport costs. While this is only an approximation, it facilitates the comparison across the various distance measures.

  47. 47.

    This is approximately the median distance to the next SEZ. The results are similar for a radius of 100. The coefficients vary more when we use a variety of different radii between 20 and 900 km, but we never find significant negative spillover effects. In robustness checks, we also computed the distance to the closest zone in the same province, and the results are qualitatively similar.

  48. 48.

    Such measures of market access or market potential appear in models of trade and economic geography, see for example Fujita et al. (1999).

  49. 49.

    Briant et al. (2015) weigh by population instead of GDP. The results are robust to using population.

  50. 50.

    For example, if several cities in the close neighborhood experience GDP growth but only one of them has a SEZ, then this measure of exposure may partly capture the general increase in market access. Although we control for province-time interactions in all of our regressions and therefore absorb much of the regional growth trends, this measure gives higher weight to close neighbors and hence may capture spatial trends at the local level.

  51. 51.

    Here TFP is constructed using the full-sample unrestricted production function estimation. The other two measures of TFP give similar results.

  52. 52.

    When we restrict the sample to the years when we have better population data from the census, then the signs of the coefficients vary and they are never significant.

  53. 53.

    Different from us, Wang (2013) finds some evidence of negative FDI spillovers in neighboring cities. A potential explanation for the difference in the results is that she does not distinguish between state-level and province-level zones and only considers the spillover effect of FDI on neighboring cities.

  54. 54.

    The strategy of estimating the effects at different levels of aggregation in order to verify the presence of spillovers from the treated location to neighboring areas is also applied in Criscuolo et al. (2012) in their analysis of place-based policies in the UK.

  55. 55.

    The positive effect may be due to firms active in SEZ setting up facilities in the periphery. To the extent to which firms do not benefit from special exemptions for the activities performed outside of the SEZ, we regard this as as a spillover. However, one might conjecture that firms located inside the SEZ can benefit from special treatment even if they locate some facilities in neighboring areas. We could not find any precise information in this regard.

  56. 56.

    Elvidge et al. (1997) are among the first to discuss the relationship between light and economic activity. See also Henderson et al. (2012) and Chen and Nordhaus (2011) and the literature cited there on the use of light to measure economic activity. Ma et al. (2012) and Hälg (2012) discuss the use of light data for Chinese cities. See also the Online Appendix for further details on the data source.

  57. 57.

    When there are no data constraints due to border changes, then the urban core is a reasonable unit of analysis, since the SEZ in our sample were located in the urban cores. The analysis using light data exploits this advantage, but we have also done the analysis for the larger definition of a city that includes the periphery, which is the unit that the baseline GDP results are based on. The effects of SEZ at that level are smaller and insignificant. We have no explanation for the difference in the result between urban core and the area that includes the periphery. It appears to be specific to the light data, since such large differences were not observed for other data.

  58. 58.

    This loss of precision is confirmed by the observation that if we run the baseline regression of Sect. 4.2 with GDP as the dependent variable for the post-1992 period we obtain a positive (0.043) but statistically insignificant point estimate.

  59. 59.

    However, we find no significant effect in the inland sample. We suspect that this is due to the poor quality of electricity data in this subsample, for which we have no explanation. We calculated the correlation between GDP and electricity separately in four sub-samples: inland reformers, inland non-reformers, coastal reformers and coastal non-reformers. The correlation is high and significant in all subsamples except for that of inland reformers, where the elasticity of GDP with respect to electricity is very low (0.02) and statistically insignificant. Interestingly, the correlation between GDP and satellite light intensity is instead consistent and significant across the four sub-samples, suggesting that the source of the problem is not the GDP statistics but rather the electricity data.

  60. 60.

    It is important to note here that the city size could vary over time, and there were changes in the administrative system. The yearbooks allow us to match the city names over the years and control for these border changes by including land area as an explanatory variable.

  61. 61.

    Please see the Online Appendix B for more detailed descriptions of the data source.

  62. 62.

    The same holds true for the capital-labor ratio and for TFP (result not shown).

  63. 63.

    The literature finds a relatively small endogeneity bias in the coefficient for population density. For example, Combes and Gobillon (2015) document that the endogeneity bias on the elasticity of density is between 10 and 20 %, sometimes the bias is close to zero and even negative. Combes et al. (2010) provide a detailed comparison of different identification strategies. In particular, they note how difficult it is to find valid time-varying instruments (most attempts in the existing literature have resulted in weak instrumentation). An example for time-invariant instruments is given in Ciccone and Hall (1996), who study the effect of density by using historical population as an instrument. Combes et al. (2008), Duranton and Puga (2004), and Glaeser and Gottlieb (2009) provide a more general discussion of spatial concentration and productivity. An example of an analysis of agglomeration forces in China is Combes et al. (2013), who use Chinese household survey data.

  64. 64.

    See for example Martin et al. (2011b) for a panel analysis where lagged variables are used as instruments.

  65. 65.

    An average city then has roughly three different fixed effects over the years because of changes in the land area variable.

  66. 66.

    We compare the characteristics to reformer cities because for some variables all reformers are above the median, such that the interaction effect would be collinear with the main effect.

  67. 67.

    The mean estimate of the placebo reform is 0.0003, and is never significant and higher than the one of the true reform.

  68. 68.

    The mean estimate of this placebo reform is 0.0911. In only 13 % of the draws does the placebo specification yield significant coefficients that are higher than the actual coefficients.

  69. 69.

    The assignment of random reform years among reformers implies that a placebo reform year is likely to coincide with the true reform year. This is the case in 36 % of the draws.

  70. 70.

    The fully flexible specification with separate indicators for each year is very demanding, and yields imprecise estimates.

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Acknowledgments

We thank Oded Galor and four referees as well as Simeon D. Alder, Thomas Chaney, Silvio Contessi, Florian Hälg, James Kung, Minho Kim, Stelios Michalopoulos, Ben Olken, Jody Ono, Janneke Pieters, Raymond Riezman, Dominic Rohner, Zheng Song, Kjetil Storesletten, Nico Voigtlaender, Xiaodong Zhu, Josef Zweimüller, as well as seminar participants at the Chinese University of Hong Kong, DEGIT XVII, Royal Economic Society Meeting, SED Meeting, Tsinghua Macro Workshop, University of Bern, University of Zurich, Washington University in St. Louis, Missouri Economics Conference, ZEW Mannheim, and UNC Charlotte. We also thank Xiaojun Chen, Florian Hälg, Lingqing Jiang, Yung-Chieh Huang, Liu Liu, Sebastian Ottinger, Matthias Schief, and Laura Zwyssig for excellent research assistance. Financial support from the European Research Council (ERC Advanced Grant IPCDP-229883) and the Swiss National Science Foundation (SCOPES Grant IZ73Z0_152730) is gratefully acknowledged. Each of the three authors declares that he or she has no relevant or material financial interests that relate to the research described in this paper.

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Correspondence to Fabrizio Zilibotti.

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Alder, S., Shao, L. & Zilibotti, F. Economic reforms and industrial policy in a panel of Chinese cities. J Econ Growth 21, 305–349 (2016). https://doi.org/10.1007/s10887-016-9131-x

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Keywords

  • China
  • Economic growth
  • Economic reforms
  • Industrial policy
  • Special economic zones
  • Productivity

JEL Classification

  • H72
  • L52
  • O25
  • O38
  • O53
  • P21
  • R11