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Innovation spillover and merger decisions

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Abstract

The merger–innovation nexus has been well studied in the theoretical literature, but empirical evidence, particularly on the spillover impacts of innovation, is limited. Merger decisions are influenced by a series of macroeconomic and behavioural factors; however, internalizing innovation spillovers and keeping a competitive edge may also explain merger activities. In this paper, we investigate the impact of innovation spillovers on the likelihood of firms to merge, using a combined panel data set of mergers among publicly traded US manufacturing firms from 1980 to 2003. Innovation is measured using R&D investments and citation-weighted patents, and innovation spillover is proxied using the technological proximity of firms and rivals’ innovation. We include a series of control variables affecting merger decisions and address the potential endogeneity problem using previous R&D activities of firms. We find that innovative firms are on average more likely to merge. The results also show that within-industry inward spillovers increase the likelihood of mergers, but between-industry inward spillovers do not influence merger decisions significantly. Our main results are robust to alternative measures of innovation and spillovers as well as to different estimation methods such as propensity score matching.

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Notes

  1. As an example, Jost and Velden (2008) point to the development of a new drug in the pharmaceutical industry, which requires large R&D investments and takes several years. The requirement for large investments in R&D has led to mergers between large companies in this industry, including GlaxoWellcome and SmithKlinee Beecham in 2001 and Hoechsr and Rhone Poulenc in 1998 among many others.

  2. The private rate of return of innovation is the benefit earned by the firm participating in the innovative activities. The social rate of return includes benefits to consumers and other firms (Jaffe 1998).

  3. There are other cooperative strategies to capture spillovers, such as research joint ventures or RJVs (Gugler and Siebert 2007; Kamien et al. 1992). Both mergers and RJVs may result in efficiency gains and market power; however, they are different in terms of their production decisions. Firms make their production decisions cooperatively in mergers, but they act independently in RJVs. RJVs also do not reduce the number of firms in the market in the same way as mergers and thus the likelihood of gaining higher market power in the case of RJVs is less acute than mergers. Gugler and Siebert (2007) show that efficiency effect dominates market power effect for both mergers and RJVs in the semiconductor industry, but mergers achieve efficiencies sooner than RJVs. Our study is focused on mergers, as we do not have information on RJVs in our data and, therefore, cannot compare the impacts of mergers and RJVs on innovation spillovers.

  4. Bena and Li (2014) also include non-merging firms in their control group and construct a technological proximity measure close to ours. However, their specification of non-merging firms and technological proxies differs from ours. They include as non-merging firms those that have participated in the merger process but whose bids were not successful during the 3-year intervals before the announcement and after the withdrawal. Thus, some firms in their control group may have experienced mergers outside of this 6-year time span. Our non-merging firms are those that did not experience a merger in the entire span of our sample; our observations of these firms are not limited to the suggested 6 years in Bena and Li (2014). For technological proximity, Bena and Li use patenting information across technological classes of PATSTAT data on target and acquirers in failed or completed mergers during the 6-year intervals. Our technological proximity measure uses the distribution of patent citations of all firms (completed mergers and non-merging firms in the entire sample) across technological classes of the USPTO for all years of the sample. Compared with the patent count, the patent citations variable is a better proxy for innovation as it reflects the quality of the patents and the benefits that a firm receives from the research activity of other firms in the same technology field (Noel and Schankerman 2013; Entezarkheir 2017).

  5. As in Noel and Schankerman (2013), the initial sample values of R&D variable is used as the initial stock of R&D. Hall and Mairesse (1995) use 15% for the depreciation rate and show that the R&D stock measure is not sensitive to changes in this parameter.

  6. The proximity measure is symmetric to the ordering of firms (\(\rho _{ij}\) = \(\rho _{ji}\)).

  7. We will also specify technological proximity based on industries rather than technology classes in Sect. 4.2.

  8. Chemicals includes chemical products; Computers includes computers and computing equipment; Drugs includes optical and medical instruments and pharmaceuticals; Electricals includes electrical machinery and electrical instrument and communication equipment; Mechanicals includes primary metal products, fabricated metal products, machinery and engines, transportation equipment, motor vehicles, and auto parts. The number of firms and the number of mergers in each industry in the sample are: Chemicals, 174/21 (12%); Computers, 337/28 (5.3%); Drugs, 1089/87 (8%); Electricals, 1250/99 (8%); Mechanicals, 866/91 (10%).

  9. Harford (2005) and Komlenovic et al. (2011) use the first principal component of \(AssetTurnover_{it}\), \(EmployGrowth_{it}\), SaleGrowth it, \(Profitability_{it}\), \(ROA_{it}\), and \(CapitalExp_{it}\) to measure industry shocks. They justify this by the high level of multicollinearity among these variables in the industry level. However, we do not find this problem at the firm-level data, and therefore we use the six variables above directly in Eq. (1). As a robustness check and for the sake of comparison, we also report our estimates of Eq. (1) with the first principal component of these variables in Sect. 4.

  10. According to Harford (2005), the regulation changes took place in 1981, 1982, 1984, 1987, 1989, and 1991–96. We also estimated Eq. (1) controlling for these regulation changes but our estimated coefficients of \( logR \& DStock_{it-1}\) and \( logSpillR \& D_{it-1}\) present a similar result.

  11. Inflation adjustments are based on the CPI urban US  index for 1992 (Source: http://www.bls.gov).

  12. Our measure of business cycle also controls for time fixed effects. We also control for time fixed effects with indicator variables for each year instead of business cycles in Sect. 4.

  13. For a detailed explanation of the series used in building the CFNAI index, see Komlenovic et al. (2011) and www.chicagofed.org/publications/cfnai/index.

  14. Another measure of business cycles previously used in the literature is the National Bureau of Economic Research (NBER) business cycles index. The reported status of the economy by the NBER dates, however, has considerable lags, which devalues the information provided for company managements in their decision-making. For example, NBER announced the trough in the business cycle of June 2009 on 20 September 2010. However, the CFNAI index is built upon economic data present at the estimation time. This information on NBER dates is available at: http://www.nber.org/cycles.html.

  15. This method of calculating market share follows Blundell et al. (1999), who employ sales in the primary SIC3, Giroud and Mueller (2010), who use sales in the primary SIC2 and SIC4; and Duso et al. (2014), who utilize sales in the primary SIC4. We would have liked to build the market share variable at a more disaggregate level, but our data only provide information at the SIC4 level. As Duso et al. (2014) note, using SIC4-level information to define market share might generate lower bound estimates, as the relevant anti-trust market might be smaller than the product markets defined by SIC4.

  16. Bronwyn Hall prepared the updated NBER patent and citation files, available at http://elsa.berkeley.edu/~bhhall/. The original files are explained in Hall et al. (2001) and their time range is from 1963 to 1999.

  17. The publicly traded firms are those traded on the New York, American, and regional stock exchanges, as well as over-the-counter in NASDAQ.

  18. The company identifier file is available at http://elsa.berkeley.edu/~bhhall.

  19. According to the USPTO’s website, withdrawn patents are those that are not issued (http://www.uspto.gov/patents/process/search/withdrawn.jsp). Note that the citation data are not limited to public firms.

  20. To correct for the truncation in patent and citation counts, we follow Hall et al. (2000) by defining a weight factor as follows:

    $$\begin{aligned} PC_{t}^*= & {} \frac{PC_{t}}{\sum _{J=0}^{2003-t} W_J} \nonumber \\ 2000\le & {} t\le 2003, \end{aligned}$$
    (6)

    where \(PC_{t}\) is the number of patents granted at time t to all firms and \(W_J\) is an index built based on the average citations in each lag for the patents granted. Lags are the differences between the last year of the sample (2003) and the ending years of the sample (2000–2003). We multiply the inverse of the weight factor (\(1/PC_{t}^*\)) by the patent counts in ending years of the sample to correct for the truncation. We apply this to years 2000–2003, because the last years of the sample (2004–2006) are subject to “edge effect”: large variances and therefore unstable. We also correct for truncation in citations data using the citations distribution between the granting year of the citing patent and the granting year of the cited patent in the patent document of the citing patent. We then forecast the number of citations that might be received for each citing patent outside the range of the sample up to 40 years after the granting date of the citation counts. For more details, see Entezarkheir and Moshiri (2018).

  21. Note that some of the acquiring firms experience several mergers during the sample period, and we keep them all in the sample.

  22. The number of replications for bootstrapped standard errors is 400.

  23. This interpretation of the results may not be robust if there is a large number of competing firms in each industry, as the acquiring firm can only internalize a very tiny portion of the knowledge spilling over to many firms. However, the median industry in our data has 14 public firms and one merger (29 firms and two mergers on average) with the HHI index of 0.28, implying that each merger may still provide access to a considerable part of the spillover pool.

  24. We also estimated the model with the second and third lags of innovation spillover variables but the results remain robust. In the case of second lag, the estimated coefficients of \( logR \& DStock_{it-2}\) and \( logSpillR \& D_{it-2}\) are 0.283 (Std.Error \(=\) 0.131) and 0.651 (Std. Error \(=\) 0.228), and in the case of third lag, the estimated coefficients of \( logR \& DStock_{it-3}\) and \( logSpillR \& D_{it-3}\) are 0.223 (Std.Error \(=\) 0.086) and 0.678 (Std. Error \(=\) 0.192), respectively. As suggested by a referee, we isolated the impact of technological proximity on the merger likelihood by removing it from the spillover measure. The estimated coefficient of spillover without technological proximity is 0.441 (Std.Error \(=\) 0.195), which is less than the original estimated values, implying that technological proximity would increase the impact of innovation spillover on mergers.

  25. One possible concern that may be raised here is that the positive correlation we find is only capturing scale effects. In other words, larger firms tend to merge more. Nevertheless, in our estimations, we control for size of firms by the variable \(EmployGrowth_{it}\) in Eq. (1). Moreover, in Sect. 4.2, we show that when we use the logarithm of R&D expenditure (\( logR \& D_{it}\)) or the logarithm of R&D intensity (\( log(R \& D/L)_{it}\)) instead of stock of R&D for measuring innovation, we still find a positive and statistically significant impact from innovation on merger likelihood.

  26. The effect of \(BC_{t}\) is also positive and significant but smaller than the \(BC_{t-1}\) effect. As a robustness check, we control for time-fixed effects instead of business cycles. The impacts of \( logR \& DStock_{it-1}\) (0.373, Std. Error=0.153) and \( logSpillR \& D_{it-1}\) (1.900, Std. Error=0.741) stay positive and statistically significant.

  27. The negative estimated coefficient of \(logHHI_{ht}\) in Column (3) indicates that higher concentration in the industry of the acquiring firms lowers the likelihood of merger. This finding conforms to anti-trust regulations that a proposed merger in a highly concentrated industry is more likely to be rejected ceteris paribus. Nevertheless, the impact is also not statistically significant.

  28. Since variables on target characteristics may be highly correlated, we also consider the first principal component of these three variables as in Harford (2005). The estimated results with the PC variable included do not change. The estimated coefficients of \( logR \& DStock_{it-1}\) and \( logSpillR \& D_{it-1}\) are 1.239 (Std.Error \(=\) 0.437) and 2.207 (Std. Error \(=\) 0.643), respectively.

  29. The number of replications for bootstrapped standard errors is 400.

  30. As a robustness check, we further estimate the model in Column (3) of Table 6 with the linear probability method. The positive impacts of spillover variables remain the same, smaller in value though. The estimated coefficients of \( logR \& DStock_{it-1}\) and \( logSpillR \& D_{it-1}\) are 0.009 (Std.Error \(=\) 0.003) and 0.019 (Std.Error \(=\) 0.004), respectively.

  31. For a list of studies on competition and innovation, see Entezarkheir and Moshiri (2018).

  32. The Wooldridge (2010) test result also confirms the endogeneity of \( logR \& DStock_{it-1}\).

  33. We apply the method outlined in Wooldridge (2010) for the test of overidentifying restrictions. We first estimate Eq. (1) and obtain predicted residuals. We then calculate \(J=MF\) from a regression of estimated residuals on instruments. The estimated test statistic is equal to 21, leading us almost not to reject the hypothesis of exogeneity of the instruments.

  34. Possible caveats to using the citation-weighted patent stock as a measure for innovation are that some firms may patent defensively, which means that they are only marginal innovations (Hall and Ziedonis 2001; Ziedonis 2004; Noel and Schankerman 2013), and not all innovations are patented. Nevertheless, our findings are robust to this measure of innovation.

  35. The bias is defined as the difference in the mean values of the treatment group and the control group, divided by the square root of the average sample variance in the treatment group and the not matched control group (Rosenbaum and Robin 1985). Our results are robust to other matching techniques, such as Kernel matching.

  36. To check for the common support condition, we compare the min and max values of the propensity score in both the target and control groups. For details on this method, see Caliendo and Kopeinig (2008).

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  1. Department of Economics, Huron University College at University of Western Ontario, 1349 Western Rd, London, ON, N6G 1H3, Canada

    Mahdiyeh Entezarkheir

  2. Department of Economics, STM College, University of Saskatchewan, 1437 College Dr., Saskatoon, SK, S7N 0W6, Canada

    Saeed Moshiri

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We are grateful for comments by Mario Samano, and by participants at the 2018 IIOC and CEA conferences, and the seminars organized by the Department of Economics, the University of Western Ontario, and the Department of Agricultural and Resource Economics, University of Saskatchewan. We would also like to thank the anonymous referee for valuable comments. The usual disclaimer applies.

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Entezarkheir, M., Moshiri, S. Innovation spillover and merger decisions. Empir Econ 61, 2419–2448 (2021). https://doi.org/10.1007/s00181-020-01973-6

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  • DOI: https://doi.org/10.1007/s00181-020-01973-6

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