Empirical Methods for Corporate Finance

Transcription

1 Empirical Methods for Corporate Finance Difference in Differences Note: This set of slides is inspired by that of Michael R. Roberts at Wharton

2 Basics (As said earlier) one of the most causes of endogeneity (violation of A3 in OLS) in empirical corporate finance is omitted variables (Refhresher) Some variable(s) that the econometrician does not observe but that is correlated with the dependent and explanatory variable(s) Mainly due to the considerable (unobserved) heterogeneity present in many corporate finance settings Firms can differ in so many ways! (think about it for one second) Difference in Differences (DD) can be a powerful tool to identify causal effects 4/23/2015 2

3 DD Intuition DD is a quasi experimental technique used to understand the effect of a sharp change in the economic environment or government policy. Butler and Cornaggia (2011) use ethanol mandates from the EPA of 2005, which require the increased use of corn in fuel, to understand the effect of access to finance on productivity of farmers Leary (2009) use changes in bank funding constraints to assess the effect of capital markets frictions on corporate capital structure decisions Used in conjunction with a natural experiment in which nature does the randomization for us Key: transparent exogenous source of variation that determines treatment assignment (e.g., policy changes, government randomization, etc.) Goal: be as close as possible to a perfect random experiment 4/23/2015 3

4 A Hypothetical Example Question: What is the effect of a decline in expected bankruptcy costs on corporate debt usage? Tradeoff theory of capital structure predicts that debt usage and expected bankruptcy costs are inversely related Ideal but Impossible Experiment: Take a set of firms, reduce bankruptcy costs (e.g., streamline bankruptcy procedures) and measure debt usage Rewind the clock, take the same set of firms and measure their debt usage Compare debt usage across two scenarios Desirable but Infeasible Experiment Take a set of firms and randomly select some fraction of firms to be subject to the new bankruptcy procedures. Compare debt usage across the two sets of firms 4/23/2015 4

5 What was Good about these Experiments? The key to causal identification is estimating the counterfactual: What would have happened had the treated not be treated? Therefore, quality of the identification is tied to how well we can estimate the counterfactual The Ideal but Impossible Experiment actually provides the counterfactual by rewinding the clock. The Desirable but Infeasible Experiment provides a good estimate of the counterfactual by the random assignment 4/23/2015 5

6 The Natural Experiment At the end of 1991, Delaware passes a law that significantly streamlines bankruptcy proceedings to make litigation less costly and time consuming Must assume that this is a random (or outcome unrelated) event. The event should not be a response to pre existing differences between the treatment and control group (e.g., Delaware firms are much more likely to enter financial distress) Must understand what caused the event to occur This law change offers a potentially useful setting with which to test our hypothesized relation between bankruptcy costs and capital structure How do we empirically test the relation? (three possibilities ) 4/23/2015 6

7 (1) Cross Sectional Difference After Treatment Idea: compare the average leverage of firms registered in Delaware to that of firms registered elsewhere This can be accomplished via a cross sectional regression where y i = Leverage for firm i in 1992, and I(treat i ) = 1 if firm is registered in Delaware Assuming E(ε i I(treat i )) = 0: E y E y i i y i 0 1 i i I treat Itreati 0 0 Itreati i i i i E y I treat 1 E y I treat 0 The estimate is just the difference in average leverage in 1992 for the treatment group (Delaware firms) and control group (non Delaware firms) 4/23/

8 Potential Concerns As usual, the concern lies with our assumption of E(ε i I(treat i )) = 0 (exogeneity of the treatment) What could threaten this assumption and, consequentially, the internal validity of the estimate? What if firms in Delaware are different (e.g. more capital intensive or more profitable) relative to firms elsewhere? Problem is that firms with more physical capital tend to be more levered so our assumption is violated because capital intensity is sitting in ε and it s correlated with treatment status In other words, even if the law was never passed, we would expect firms in Delaware to have higher leverage then other firms because of genuine unobserved differences between firms in Delaware and elsewhere 4/23/2015 8

9 What to Do? One Solution Insert control variables (e.g., net plant, property, and equipment divided by assets) in the regression But, these are just proxies There is still some heterogeneity between treatment and control groups that is sitting in the error term and might be correlated with our treatment indicator Unfortunately, unobserved differences can subsist (unless we can find an instrument ) 4/23/2015 9

10 (2) Time Series Difference Within the Treatment Group Idea: compare the average leverage of firms registered in Delaware in 1991 to that in 1992 avoids heterogeneous firm concern This can be accomplished via a two period panel regression using only Delaware firms y it 0 1 it it where I(Post) = 1 if year = 1992 and 0 if year = I Post Assuming E(ε it I(Post it )) = 0: E y E y it it IPostit 0 0 IPostit it it it it E y I Post 1 E y I Post 0 Our estimate is just the difference in average leverage for Delaware firms in 1992 (the post treatment era) and 1991 (the pre treatment era) Consider the cross sectional, first difference regression y 4/23/ it 1 1 it

11 Potential Concerns The primary concern here is other factors affecting leverage over time. E.g., Increase in the supply of credit due to financial innovation Leverage would likely have increased for firms even without the passage of the law Bias is positive in favor of supporting a treatment effect This is just another form of omitted variables bias, as before We could insert control variables but difficult to measure all perfectly Also, bias can work in both directions E.g., 1992 may be a period of tight credit, which leads to a decline in debt usage and offsetting effect 4/23/

12 Difference in Differences Estimator Simple (natural) idea: Combine the positive features of each single difference estimator Cross sectional estimator avoids omitted unobserved common trends Time series estimator avoids omitted unobserved cross sectional differences The DD estimator does precisely that! This is the DD estimator! y I treat I post I treat I post it 0 1 it 2 it 3 it it it We need a full panel of firms consisting of Delaware (I(treat) = 1) and Non Delaware (I(treat) = 0) registered firms observed before (I(post) = 0) and after (I(post) = 1) the passage of the law 4/23/

13 How is β 3 the DD estimator? Compute the conditional expectations E y I treat 1, I Post 1 it it it Take difference over time in average leverage for control group and subtract from difference over time in average leverage for treatment group E y I treat 1, I Post 0 it it it E y I treat 0, I Post 1 it it it E y I treat 0, I Post 0 it it it E yit I treatit 1, I Postit 1 E yit I treatit 1, I Postit Average Leverage for Delaware firms in 1992 Average Leverage for Delaware firms in Difference in Average Leverage for Delware Firms E yit I treatit 0, I Postit 1 E yit I treatit 0, I Postit Average Leverage for Non-Delaware firms in 1992 Average Leverage for Non-Delaware firms in Difference in Average Leverage for Non-Delware Firms /23/

14 Conditional Mean Estimates Easier to see what the parameters estimate by arranging things in a 2 x 2 matrix: Treatment Control Difference Post Pre Difference Note: Implies alternative route to DD estimator: subtract difference in average leverage for treatment and control in 1991 from the difference in average leverage for treatment and control in 1992 β 1 is the average leverage of treatment firms in the pre treatment era relative to (i.e. minus) the average leverage of control firms in the pre treatment era β 2 is the average leverage of control firms in the post treatment era relative to (i.e. minus) the average leverage of control firms in the pre treatment era 4/23/

15 Re Visiting the Single Difference Estimators Cross sectional difference: 1 3 E y I treat 1, I post 1 E y I treat 0, I post 1 Unbiased if β 1 is equal to zero no permanent difference between the treatment and control groups Time series difference: 2 3 E y I treat 1, I post 1 E y I treat 1, I post 0 Unbiased if β 2 is equal to zero no common trend over the pre and posttreatment eras DD estimator avoids these two threats by differencing away any permanent differences between the groups and any common trend affecting both groups 4/23/

16 Key Assumption Behind DD In the absence of treatment, the average change in the response variable would have been the same for both the treatment and control groups. Similar to the parallel trends assumption since it requires that the trend in the outcome variable for both treatment and control groups during the pre treatment era are similar. What this assumptions does not mean It does not mean that the there is no trend in the outcome variable during the pre treatment era (just the same trend across groups) It does not require that the level of the outcome variable for the two groups be same in the pre treatment era 4/23/

17 Testing the Key Assumption Behind DD Strictly speaking, this is untestable. It s just saying that E(ε I(treat) x I(post)) = 0 and we don t observe ε But, we can inspect pre treatment era growth rates in outcome variables (By definition, this requires more than two periods of data) What we need to have What we must not have β 3 can be significant (but not causal) 4/23/

18 Graphical Analysis A nice DD picture of our bankruptcy law experiment Similar leverage growth (~0) in pre-treatment era Bonus: Similar leverage level (~30%) in pretreatment era Leverage Event Year Sharp change in leverage for treatment group right after event No change in leverage after event for control group Treatment Control 4/23/

19 Statistical Analysis We could also perform a t test of the difference in average leverage growth rates across the treatment and control groups during the pre treatment era. This should turn out insignificant (statistically and economically) if the parallel trends assumption is valid Statistical insignificance is not enough could be low power You should be skeptical of any DD that doesn t show you a picture or an explicit test of this assumption. Of course, this requires sufficient data on pre treatment outcomes 4/23/

20 Level Regression Estimates Remember: β 1 = Avg. leverage of treatment group in pretreatment era less avg. leverage of control group in pre treatment era β 2 = Avg. leverage of control group in posttreatment era less avg. leverage of control group in pre treatment era β 3 = DD estimate β 0 = Avg. leverage of control group in the pretreatment era Note: Single difference estimators will give you basically same result since β 1 = β 2 = 0 (i.e., no time invariant differences between groups or common trends across groups) Back out conditional means via linear combinations of parameters (e.g., avg. leverage of treatment group in pre treatment era = β 0 + β 1 = 29% Reconcile estimates with figure β 1 : I(treat) (-0.673) β 2 : I(post) (0.296) β 3 : I(treat) x I(post) 0.206** (14.939) β 0 : Intercept 0.299** (43.403) Observations 5,000 Fraction Treatment Adjusted R /23/

21 Sensitivity Tests I Redo the DD analysis on pre event years (The estimated treatment effect should be zero) Multiple control groups (E.g., define control groups to be firms in adjacent states) For the these previous two sensitivity tests, we could do a triple diff: Difference in difference in differences DD in dif estimated difference between DD of interest and the other DD. But, If the other DD is zero, doing a triple dif will only work to inflate the standard errors. If the other DD is not zero, you have to wonder whether the original DD is unbiased Compare treatment and control groups along various covariates to see if they are similar, at least along observable dimensions 4/23/

22 Sensitivity Tests II Make sure change is concentrated around the event (Identification is coming from exogenous event) Make sure other outcome variables that should be unaffected by the event are actually unaffected Control by systematic variation (See if treatment and control groups respond to other factors similarly (Rosenbaum (1987)) Multiple treatment groups E.g., If Delaware implemented the changes in three stages, one could define separate control groups corresponding to each stage E.g., could separate out levered from unlevered firms in order to focus on firms most likely to be affected by the change. Treatment Reversal (If the new law is repealed, do we see a reversal of the effect? (e.g., Leary (2008)) Use robust (to heteroskedasticity and, more importantly, dependence) SEs Bertrand, Duflo, and Mulainathan (2004), Petersen (2009), Donald and Lang (2007) 4/23/

23 Summary DD can be a simple but powerful empirical strategy Relies crucially on: Exogeneity and sharpness of the event/treatment Comparability of the treatment and control groups As with many empirical papers, a picture is worth a thousand words Like other quasi experimental methods, should be accompanied by a battery of robustness tests ensuring internal validity As with all natural experiments and quasi experimental methods, extrapolation is tricky Take care in extrapolating the results Internal validity is often inversely related to external validity 4/23/

24 Application 1: Monitoring and Investment Giroud, 2013, Proximity and Investment: Evidence from Plant Level Data (Quarterly Journal of Economics) Question: How does proximity to headquarter affect plants investment and productivity? Motivation: No existing evidence on the role of proximity for firms internal decisions (evidence for arm length relation such as banking or mutual fund investment) Empirical Strategy: Use introduction of new airline routes as exogenous reduction in travel time, and hence an increase in proximity Results: Proximity matters! Higher investment and higher TFP! 4/23/

25 Location in the field Governance Real decisions Financing Valuation Institutional framework: laws, regulations, taxes, markets, macro economy 4/23/

26 Plant level Data Manufacturing plant data from US Census ( ) Identification of HQ and all the plants of a given firm Single and multi units firms Addresses of all plants (establishements) 1.3 million plant year observations 4/23/2015 Empircal Corporate Finance 26

27 Air travel data Include all flights that have taken place between two airports in the US Monthly data for each airline and route (e.g. United Boston Memphis) Origin, destination airports, flight duration, and aircraft type 4/23/2015 Empircal Corporate Finance 27

28 Travel time Assumption: Managers use the shortest travel time Travel time between two ZIP codes (HQ and plant) Compute travel time by car Find the fastest airline route between two ZIP codes (1) Time by car between HQ and origin airport (2) Duration of the flight (including layover) (average across all flight) (3) Time by car between destination airport and plant Assumption: 1 hour at airports (including layover) 4/23/2015 Empircal Corporate Finance 28

29 Summary Statistics 4/23/2015 Empircal Corporate Finance 29

30 Empirical Strategy: Example 4/23/2015 Empircal Corporate Finance 30

31 Empirical Strategy: Example 4/23/2015 Empircal Corporate Finance 31

32 Specification Difference in Differences specification: iis plant, j is firm, l is location and t is time treatment=1 if new route reducing travel time between plant and HQ has been introduced by time t H0: New route introduction does not matter (β=0) Treated group: Plant experiencing a decrease in travel time (5 years before and 5 years after) Control group: All the other plants (business as usual) 4/23/2015 Empircal Corporate Finance 32

33 Travel time reduction for Treated firms 4/23/2015 Empircal Corporate Finance 33

34 Identification Challenges New routes are endogenous Could depend on local conditions (booming economy) This could also be related with plant investment Omitted variable problem BUT treatment is uniquely defined by two airport locations Compare Boston (HQ) Memphis (Treated) with Chicago (HQ) Memphis (Control) MSA Year controls (mean of independent variable) Include firm year controls (whole firm) to capture firm level shocks (e.g. the whole firm investment more in a given year) Plant level shocks (new route because the plant is booming) Look at investment before the event and find nothing significant 4/23/2015 Empircal Corporate Finance 34

35 Main Results 4/23/2015 Empircal Corporate Finance 35

36 Dynamic Effect 4/23/2015 Empircal Corporate Finance 36

37 Heterogeneity 4/23/2015 Empircal Corporate Finance 37

38 Heterogeneity 4/23/2015 Empircal Corporate Finance 38

39 Application 2: Credit supply and leverage Leary, 2009, Bank loan supply, lender choice, and corporate capital structure (Journal of Finance) Question: Are capital market frictions relevant for capital structure? Motivation: The interactions between capital markets and firms decisions are not well understood (no connection in a MM world) Empirical challenge: observed leverage is determined by the demand and supply factors. It is difficult to isolate either demand or supply changes Empirical strategy: Use a natural experiment and a difference indifferences methodology to make a causal statement on the effect of credit supply on leverage Results: Capital structure is largely affects by exogenous change in the supply of credit 4/23/

40 Location in the field Governance Real decisions Financing Valuation Institutional framework: laws, regulations, taxes, markets, macro economy 4/23/

41 A bit of theory Why would changes in the amount of credit flowing through the banking system influence corporate leverage ratios? Loans may not be perfect substitutes for other assets held by banks. So an outflow of deposit may lead to a reduction in loan supply, not simply a rebalancing of bank portfolios Firms may not be able to freely and costlessly substitute among debt sources (asymmetric information create debt market segmentation) These assumptions are at the heart of the paper! They need to be checked for the experiment to make sense 4/23/

42 Two natural experiments 1960: The emergence of Banks certificates of deposits (CD) Corporation became more adept at cash management and moved cash from noninterest bearing bank deposits to money market instruments Shrinkage of banks deposit base February 1961, first large denomination negotiable CD. Large expansion of their loan portfolio 1966: Credit crunch Generated by different factors. Large outflows from banks («desintermediation») These events represents an expansion and contraction of banks credit supply 4/23/

43 Empirical specification Difference in differences specification: Dummy that equals 1 after the event Identification conditions: Dummy that equals 1 for treated (small firms) (1) Clear change in credit supply (OK) (2) Supply shock should be more pronounced in the bank loan market than in other markets (equity and bond) (3) There should be no other forces causing differential changes in capital structure from the pre to post event period 4/23/

44 Was loan supply really affected? Large increase in Time deposits (deposit base) Large increase in bank loans (over other sources) 4/23/

45 Is the shock concentrated in banks? More savings flew into banks compared to non bank after the expansion shock More savings flew out of banks compared to non bank after the contraction shock 4/23/

46 Parallel trends? No difference in leverage trends between large and small firms before the event No concerns here (Good!) 4/23/

47 Supply vs Demand Effects? Is the effect driven by an increase in demand for loans by treated firms? Look atinvestment opportunities (market to book ratio) Apparently, no demand effect (the reverse actually after the crunch) 4/23/

48 Useful summary statistics 4/23/

49 DD Results 4/23/

50 Impact on financing choices? Less use of alternative sources of funding after the shock Increased used of bank debt after the credit expansion Decreased used of bank debt after the credit contraction 4/23/

51 Prevalence? DiD Source: Bowen, Fresard, and Taillard (2014) 4/23/