BENIGN NEGLECT OF COVENANT VIOLATIONS: BLISSFUL BANKING OR IGNORANT MONITORING?

Colonnello, Stefano; Koetter, Michael; Stieglitz, Moritz Article — Published Version BENIGN NEGLECT OF COVENANT VIOLATIONS: BLISSFUL BANKING OR IGNORANT MONITORING? Economic Inquiry Provided in Cooperation with: John Wiley & Sons Suggested Citation: Colonnello, Stefano; Koetter, Michael; Stieglitz, Moritz (2020) : BENIGN NEGLECT OF COVENANT VIOLATIONS: BLISSFUL BANKING OR IGNORANT MONITORING?, Economic Inquiry, ISSN 1465-7295, Wiley Periodicals, Inc., Boston, USA, Vol. 59, Iss. 1, pp. 459-477, https://doi.org/10.1111/ecin.12930 This Version is available at: https://hdl.handle.net/10419/233725 Standard-Nutzungsbedingungen: Die Dokumente auf EconStor dürfen zu eigenen wissenschaftlichen Zwecken und zum Privatgebrauch gespeichert und kopiert werden. Sie dürfen die Dokumente nicht für öffentliche oder kommerzielle Zwecke vervielfältigen, öffentlich ausstellen, öffentlich zugänglich machen, vertreiben oder anderweitig nutzen. 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STEFANO COLONNELLO, MICHAEL KOETTER and MORITZ STIEGLITZ∗ Theoretically, bank’s loan monitoring activity hinges critically on its capitalization. To proxy for monitoring intensity, we use changes in borrowers’ investment following loan covenant violations, when creditors can intervene in the governance of the firm. Exploiting granular bank-firm relationships observed in the syndicated loan market, we document substantial heterogeneity in monitoring across banks and through time. Better capitalized banks are more lenient monitors that intervene less with covenant violators. Importantly, this hands-off approach is associated with improved borrowers’ performance. Beyond enhancing financial resilience, regulation that requires banks to hold more capital may thus also mitigate the tightening of credit terms when firms experience shocks. (JEL G21, G32, G33, G34) I. INTRODUCTION Loan monitoring and screening qualify banks as information producers and informed lenders. Numerous empirical determinants of monitoring have been explored, ranging from loan characteristics to business cycle conditions (Becker, Bos, and Roszbach forthcoming; Cerqueiro, Ongena, and Roszbach 2016; Gustafson, Ivanov, ∗We thank Hans Degryse, Tim Eisert, Rüdiger Fahlenbrach, Iftekhar Hasan, Christoph Herpfer, Björn Imbierowicz, Artashes Karapetyan, David Martinez-Miera, William L. Megginson, Esteban Prieto, Stefano Rossi, Farzad Saidi, Linda Schilling, Sascha Steffen, Nathanael Vellekoop, and seminar participants at the Halle Institute for Economic Research, Deutsche Bundesbank, the IWH Financial Markets & SAFE Winterschool (Riezlern), the 6th EFI Workshop (Brussels), and the 2018 FINEST Autumn Workshop (Pordenone) for helpful discussions and comments. Special thanks go to Felix Noth for sharing data on banks’ exposures to the U.S. deposit insurance reform of 2008. Felix Klischat provided excellent research assistance. Part of this research was completed while S.C. was a Visiting Junior Fellow at Collegio Carlo Alberto under the Long-Term Investors@UniTO initiative, whose research support is gratefully acknowledged. Colonnello: Assistant Professor, Department of Economics, Ca’ Foscari University of Venice, 30121 Venice, Italy. Financial Markets Department, Halle Institute for Economic Research (IWH), Halle, Germany. E-mail [email protected] Koetter: Professor, Financial Markets Department, Halle Institute for Economic Research (IWH), Halle, Germany. Faculty of Economics and Business, Otto-von-Guericke University Magdeburg, Magdeburg, Germany. Financial Stability Division, Deutsche Bundesbank, Frankfurt, Germany. E-mail [email protected] Stieglitz: Professor, Financial Markets Department, Halle Institute for Economic Research (IWH), Halle, Germany. E-mail [email protected] and Meisenzahl forthcoming). But bank funding received little attention despite being a potentially crucial supply-side driver of monitoring. We fill this void by studying empirically banks’ monitoring activity conditional on their capital (and debt) structure. The relationship between a bank’s reliance on equity capital and monitoring activity over loans is ex ante ambiguous. Equity may induce more intense monitoring if it mitigates moral hazard problems that entail too little effort by banks to exert scrutiny due to limited liability and reliance on deposit funding (Allen, Carletti, and Marquez 2011). Such a problem is mitigated by market discipline inducing banks to hold equity capital, which typically exceeds minimum regulatory requirements. Several other theoretical papers also predict a positive link between bank capitalization and monitoring intensity (Coval and Thakor 2005; Holmstrom and Tirole 1997; Jayaraman and Thakor 2014; Mehran and Thakor 2011). More generally, the “equity monitoring hypothesis” (Schwert 2018) ABBREVIATIONS BoA: Bank of America CCM: Center for Research in Security Prices/ Compustat Merged OLS: Ordinary Least Squares PPE: Property, Plant, and Equipment RDD: Regression Discontinuity Design ROA: Return on Assets SCAP: Supervisory Capital Assessment Program SNC: Shared National Credit Program 459 Economic Inquiry (ISSN 0095-2583) Vol. 59, No. 1, January 2021, 459–477 doi:10.1111/ecin.12930 Online Early publication August 6, 2020 © 2020 The Authors. Economic Inquiry published by Wiley Periodicals LLC on behalf of Western Economic Association International. This is an open access article under the terms of the Creative Commons Attribution-NonCommercial License, which permits use, distribution and reproduction in any medium, provided the original work is properly cited and is not used for commercial purposes. 460 ECONOMIC INQUIRY posits that bank capital alleviates the moral hazard problems inherent to the banking business by giving managers more “skin in the game” and thus motivating them to screen and monitor borrowers more diligently. Alternatively, equity may reduce the bank’s incentives to monitor and intervene in the governance of the borrowing firm. Less capitalized banks may face binding increased capital charges if borrowers become troubled and have thus an incentive to monitor them closely. By contrast, a well-capitalized bank may not need to restrict borrowers’ action set through monitoring, because it has a sufficiently large equity cushion to absorb increased capital requirements. We are not aware of formal theories that formulate exactly this “equity buffer hypothesis”, but a similar conjecture is put forward by Chava and Roberts (2008). This argument mirrors the one developed by Chodorow-Reich and Falato (2018): a tougher bank’s stance may reflect not only borrowers’ but also the bank’s declining financial health. By them same token, a better capitalized lender will be more lenient during borrowers’ distress. We evaluate these two alternative hypotheses using the U.S. syndicated loan market as a laboratory. Syndicated loans are a primary source of funding for U.S. corporations, with a volume of $2.4 trillion in 2017 (Sufi 2007).1Given pervasive reforms pertaining to capital and liquidity regulation (Hancock and Dewatripont 2018), we focus on relating monitoring intensity to bank funding structure measures in general and the role played by regulatory capital in particular. Following Chava and Roberts (2008) we link syndicate banks to U.S. corporations to measure bank monitoring between 1994 and 2012. They show that borrowing firms cut investment after covenant violations because creditors intervene with the management of borrowers. Covenant violations provide a useful setting to study bank monitoring because they trigger a transfer of control rights from shareholders to creditors. We document substantial cross-sectional and time-series variation in bank monitoring. Risk-adjusted Tier 1 capital ratios exhibit a statistically significant and large relationship with our monitoring metric. Better capitalized banks adhere to a more lenient monitoring stance towards troubled borrowers, which is associated with improved borrower performance. 1. See https://www.reuters.com/article/us-uslendingrecords/u-s-syndicated-lending-topples-records. Well-capitalized banks appear to permit borrowers the pursuit of value-increasing projects also when they violate a covenant. The result that better capitalized banks adhere to a “hands-off” approach after covenant violations contradicts the argument that equity favors monitoring by giving bankers more “skin in the game.” Instead, larger equity buffers seem to permit banks to smooth negative shocks of borrowers and avoid to constrain corporate investment policy. Improved borrower performance points, in turn, to an efficiency-enhancing role of bank equity rather than to a lender distraction story. Whereas it is commonplace to considerable monitoring a desirable activity, it can also be too much of a good thing. Carletti (2004) shows theoretically under which circumstances banks monitor borrower too much. Hence, a lack of equity capital may induce banks to demand inefficient investment cuts, a form of excessive monitoring. To support a causal interpretation of this result, we exploit a quasi-experiment that provides plausibly exogenous variation in bank equity capital. The Supervisory Capital Assessment Program (SCAP or stress test) of 2009 forced a number of U.S. banks to issue equity immediately after the publication of results. We use this episode as a positive unanticipated shock to bank capitalization. The increase in equity induced banks to keep a looser monitoring stance in the years after the stress test. Thus, regulatory equity appears to “buffer” shocks and allows a benign treatment of covenant violators. Another important facet of funding structure is the composition of its debt. Existing theories focus on the distinction between deposits and other forms of debt. Calomiris and Kahn (1991) and Diamond and Rajan (2001) argue that the threat of bank runs by depositors disciplines bankers. Therefore, banks relying heavily on deposit funding would have more incentives to monitor in our context (the “fragility monitoring hypothesis” in Schwert 2018).2The same economic mechanism may be at work for banks highly exposed to rollover risk on the wholesale short-term funding market. We do not find evidence that predicting larger exposures to creditor runs induces bankers to exert more monitoring effort. Banks with a more fragile debt structure, that is, characterized by a 2. Acharya, Mehran, and Thakor (2016) consider both the bright (loan monitoring) and the dark side (risk-shifting) of debt for banks, concluding that this trade-off can lead to multiple equilibria. COLONNELLO, KOETTER & STIEGLITZ: BENIGN NEGLECT OR BLISSFUL BANKING? 461 higher reliance on deposit or short-term funding, do not monitor their borrowers significantly more intensely after covenant violations. We conclude that well-capitalized banks seem to be the more patient monitors that are less likely to impose inefficient investment cuts on borrowers. This result complements existing theories (e.g., Holmstrom and Tirole 1997), which focus on bankruptcy rather than on covenant violations (i.e., technical defaults). In contrast to bankrupt firms, covenant violators appear to be sufficiently healthy to survive certain shocks. Heavy-handed creditor interventions after violations may therefore, in fact, destroy value. This paper contributes to three strands of the literature. First, it relates to studies on the effect of covenant violations on corporate policies, such as investment (Chava and Roberts 2008), financing (Roberts and Sufi 2009), governance (Nini, Smith, and Sufi 2012), employment (Falato and Liang 2016), and board structure, see Ferreira, Ferreira, and Mariano (2018) for this last point and an overview of this literature. We study (bank) heterogeneity in creditor-induced investment reactions to covenant violations, which we use as a measure of bank monitoring intensity.3 Moreover, we investigate how covenant-violation induced investment reactions relate to changes in performance around the same events. We believe that the joint analysis of reactions of corporate policies to violations as opposed to the investigation of single measures in isolation is an important avenue to better understand the role of creditors in the governance of borrowing firms. Second, we relate to empirical studies linking heterogeneity in bank monitoring to syndicate structure (Sufi 2007), collateral values (Cerqueiro, Ongena, and Roszbach 2016), securitization (Wang and Xia 2014), and business cycle conditions (Becker, Bos, and Roszbach forthcoming). Besides providing an overview of the literature, Gustafson, Ivanov, and Meisenzahl (forthcoming) use confidential regulatory syndicated loan data from the Shared National Credit (SNC) program to show that higher lead arranger shares, shorter loan maturities, private borrowers, and a smaller number of covenants lead to higher monitoring effort. By contrast, Plosser and Santos (2016) use expanded SNC data and find that a bank’s role in the syndicate does not affect monitoring intensity. According to them, monitoring effort is determined by 3. Roberts (2015) relates renegotiation outcomes after violations to aggregate banking sector leverage. the economic exposure of a bank, that is, the absolute value of a bank’s individual loan share relative to a bank’s size. We contribute to this literature by exploring the role of banks’ funding structure for monitoring heterogeneity. Our findings clearly underpin that bank capitalization is a crucial supply-side determinant of monitoring compared to other bank traits, such as the bank’s debt structure, business model, and efficiency. Third, our paper complements the literature that links observable financial health indicators of lenders to borrower actions. Murfin (2012) shows that better capitalized banks design looser covenants. Whereas he considers equity-induced bank heterogeneity in loan contracting, we investigate how capitalization influences bank heterogeneity in responses to covenant violations. The studies most closely related to ours are Chodorow-Reich and Falato (2018) and Acharya et al. (forthcoming). Both use changes in bank balance sheet characteristics during the financial crisis to explain heterogeneity in bank responses to covenant violations. Using SNC data, Chodorow-Reich and Falato (2018) show that during the financial crisis lenders used covenant violations as an opportunity to cut credit exposure that otherwise would have been hard to reduce given loans’ high average maturity. Acharya et al. (forthcoming) corroborate the findings of Chodorow-Reich and Falato (2018) using publicly available data on credit lines. These two studies examine one extreme of the whole spectrum of monitoring that we are considering. During a crisis, distressed banks may be less interested in intervening in the borrowing firms’ management but rather want to implement lump-sum cuts in their loan book. Our study tests whether bank funding structure explains differences in monitoring looking over the entire business cycle, mitigating external validity concerns. Our results may thus provide guidance to policy-makers interested in designing regulation that brings banks closer to the optimal level of monitoring effort. II. EMPIRICAL APPROACH We explain the economic intuition why and the empirical methods how we measure monitoring intensity in the context of covenant violations before relating it to bank traits. A. Bank Monitoring and Covenant Violations The main goal of our analysis is to study how a bank’s monitoring effort correlates with its 462 ECONOMIC INQUIRY characteristics, insulating their role from that of the borrowing firm’s characteristics. Bank monitoring activity is inherently elusive. Most studies therefore measure it indirectly, assuming that certain features of the bank– borrower relationship (e.g., closer geographical distance or loan concentration among syndicate members) are conducive to more intense monitoring (see, e.g., Sufi 2007). Other, more recent studies take a different approach and look at observable monitoring activities.4 These approaches focus either on specific loan characteristics linked to monitoring effort (e.g., the lead bank’s share in syndicated loans) or on specific monitoring actions (e.g., collateral reviews). We follow a different route and reverse engineer banks’ monitoring intensity starting from the effect of their actions on borrowing firms’ policies. A main challenge is to impute changes in borrowing firms’ policies to banks’ monitoring actions. Our approach is to consider events when banks are likely to take monitoring actions. In line with Bird et al. (2017), we use changes in borrowing firms’ investment policy around violations of financial covenants contained in syndicated loan contracts as a proxy for banks’ monitoring intensity. Financial covenants set limits on accountingbased measures of financial health and performance (e.g., on net worth or current ratio) of borrowing firms. Loan covenants are commonly maintenance-based. Debtors must comply with the limits set in the loan contract at the end of each fiscal quarter (Nini, Smith, and Sufi 2012). A covenant violation constitutes a technical default, after which the creditors can impose the immediate repayment (acceleration) or the termination of the loan. Creditors mostly use the threat of such actions to renegotiate the debt contract and extract concessions from borrowers (Roberts 2015). According to the theoretical work by Gorton and Kahn (2000) and Berlin and Mester (1992), monitoring entails renegotiating loan terms upon the arrival of new information about the firm’s prospects. In their models, covenants and their violation are a mechanism to institutionalize regular renegotiations. After a violation, a lender 4. Gustafson, Ivanov, and Meisenzahl (2020) look at banks’ meetings with borrowers and on-site visits. Cerqueiro, Ongena, and Roszbach (2016) and Becker, Bos, and Roszbach (2019) measure monitoring as the frequency of borrowers or collateral reviews. Plosser and Santos (2016) infer monitoring activity from changes to banks’ internal borrower ratings. can choose to liquidate certain projects of the borrower to prevent risk-taking. This is exactly what we are measuring in the form of restrictions on firm investment. More broadly, Nikolaev (2018) defines monitoring as both acquiring timely information about borrowers and acting upon that information to exert control on management. While monitoring measures such as loan reviews (Plosser and Santos 2016), site visits, and borrower meetings (Gustafson, Ivanov, and Meisenzahl forthcoming) entail only the first part of that definition, our measure incorporates both parts because the lender has to acquire information to detect the violation. Chava and Roberts (2008) and Nini, Smith, and Sufi (2012) provide both anecdotal and large sample evidence consistent with increased monitoring following covenant violations (e.g., through increased frequency of required compliance reports). Whereas the change in investment policy linked to the resolution of the technical default can reflect a host of bank-side actions (typically changes in loan terms—interest rate, maturity, credit line availability, etc.—that make the borrower more financially constrained), it seems sensible to think that such actions capture also “pure” monitoring. In sum, covenant violations provide a useful setting to study banks’ monitoring activity for three reasons. First, they give a specific channel through which creditors can intervene in the governance of the borrowing firm, namely a formal transfer of control rights from shareholders to creditors. Second, covenant violations are widespread and involve also relatively healthy firms, thus providing a more complete picture of the role of creditors in borrowing firms (Nini, Smith, and Sufi 2012). Third, the management of borrowing firms’ only has limited ability (and incentives) to manipulate the firm’s accounting ratios to avoid covenant violations (Roberts and Sufi 2009). This feature and the discrete nature of covenant violation around the covenant threshold lend themselves to a regression discontinuity design (RDD), commonly used in the literature starting from Chava and Roberts (2008), which we discuss below more in detail. B. Investment and Covenant Violations As a preparatory analysis, we study the behavior of violating firms’ investment around covenant violations without conditioning on the lender. The goal is to link our core analysis on observable differences in bank funding structure described below to the contraction in investment COLONNELLO, KOETTER & STIEGLITZ: BENIGN NEGLECT OR BLISSFUL BANKING? 463 commonly observed in the literature (Chava and Roberts 2008). The borrowing firm’s treatment status (violating vs. nonviolating) exhibits a discontinuity with respect to the distance between the observed accounting ratio and the contractual covenant threshold. We exploit this discontinuity for identification purposes in a RDD at the firm-quarter level in the spirit of Chava and Roberts (2008) to isolate the effect of financing frictions on investment as follows5: If,q=𝛼⋅vf,q−1+𝜼xf,q−1+𝜻pf,q−1 (1) +𝛾f+𝛾q+ϵ f,q, where fand qdenote the borrowing firm and the (quarterly) period. If,qis the firm’s investment rate. The treatment variable is the firm-quarterlevel covenant violation indicator vf,q−1defined as (2) vf,q−1=⎧ ⎪ ⎨ ⎪ ⎩ 1ifzf,q−1−z0 f,q−1<0 for any covenant in loans of firm f 0 otherwise, where zf,q−1is the observed value of the accounting measure restricted by the covenant and z0 f,q−1 is the most binding covenant threshold contained in any of the firm’s outstanding syndicated loan contracts. In this firm-quarter-level analysis, vf,q−1equals one if the firm violates any covenant in any of the outstanding loans. For a given accounting measure, the relative distance (zf,q−1−z0 f,q−1)∕z0 f,q−1is defined with respect to the tightest covenant threshold across the different outstanding loans at a given point in time. Thus, the assignment variable is the relative distance between the actual accounting measure and the threshold. Hence, a violation is not more severe simply because the level of the accounting measure and the corresponding threshold are relatively high to begin with. We control for a vector of covariates xf,q−1 including Tobin’s q, the contemporaneous cash flow, and the natural logarithm of total assets of the borrowing firm. We use a second-order polynomial of the relative distance of the different accounting measures from the tightest covenant 5. This analysis is a sharp RDD because of the deterministic assignment rule into treatment and non-treatment. A caveat is that banks and firms can renegotiate the contract in anticipation of a violation. See Denis and Wang (2014) on firm policies after renegotiations outside of actual covenant violations. threshold to specify a vector of smooth functions pf,q−1(Gelman and Imbens 2018). The inclusion of pf,q−1improves the identification of the treatment effect 𝛼around the discontinuity and captures any information these distance measures may convey about the firm’s growth prospects (Falato and Liang 2016). Firm (𝛾f) and time (𝛾q) fixed effects absorb time-invariant differences in investment policy across borrowing firms and macroeconomic conditions. Error terms 𝜖f,qare clustered at the firm-level. We repeat the analysis of investment around covenant violations, but treat each syndicated loan as a set of separate loans, one for each bank in the syndicate. The unit of observation is the loan-bank-firm-quarter, so that we can focus on the heterogeneity in investment responses depending on the bank from which the firm borrowed. We use this setting in our main analysis below and execute a RDD specified as follows: Il,b,f,q=𝛼⋅vl,q−1+𝜼xf,q−1+𝜻pl,q−1 (3) +𝛾b,y+𝛾f+𝛾q+𝛾e+ϵ l,b,f,q, where l,b, and ydenote the syndicated loan deal, the lending bank, and the year, respectively. We add bank-year (𝛾b,y) and fiscal quarter (𝛾e)fixed effects to control for time-varying heterogeneity in investment across different banks’ borrowers outside covenant violations and seasonality, respectively. The treatment variable is the loanquarter-level covenant violation indicator vl,q−1 defined as (4) vl,q−1=⎧ ⎪ ⎨ ⎪ ⎩ 1ifzf,q−1−z0 l,q−1<0 for any covenant in loan l 0 otherwise, where the difference relative to the firm-quarterlevel indicator (2) lies in the covenant threshold z0 l,q, which is now loan-specific.6In this setting, vl,q−1is equal to one if the firm violates any of the covenants contained in a given loan. Analogously to (1), we include a vector of smooth functions pl,q−1of the relative distance between the different accounting measures and the loan-level covenant-threshold. As before, we only observe borrowing firms’ investment at the firm-quarterlevel and the notation Il,b,f,qreflects the repetitive 6. Thus, we do not need to focus on the tightest covenant. Time-subscripts indicate dynamic covenant thresholds. Current ratio thresholds might increase over time and net worth thresholds might increase with net income. As in Chava and Roberts (2008), we linearly interpolate initial and final covenant thresholds over the life of the loan. 464 ECONOMIC INQUIRY nature of our data structure. Because of this feature, we use two-way clustering by bank and time in the error term 𝜖l,b,f,qin line with Schwert (2018).7 In both specifications (1) and (3), the parameter 𝛼captures the treatment effect. The RDD allows us to identify the treatment effect as long the error terms (𝜖f,qor 𝜖l,b,f,q) do not exhibit the same discontinuity with respect to the threshold distance as the treatment variable (Falato and Liang 2016). We follow Chava and Roberts (2008) and estimate both specifications (1) and (3) without firms that never violate any covenant, but deviate slightly in the definition of the sample of violating firms and of the violation indicator (vf,q−1 or vl,q−1). First, we remove loans for which the firm is in violation in all quarters of their lifetime.8Second, we do not consider covenant violations as events that happen right at the beginning of a loan’s lifetime. This approach allows us to improve comparability in terms of covenant design within our sample of loans by excluding those loans that are characterized by very strict covenants. Third, once a firm violates a covenant for the first time for a given loan, we require at least four quarters without a violation before we code another breach as a “new violation” in the same spirit as Nini, Smith, and Sufi (2012). In this way, we aim to capture instances in which there is an actual transfer of control rights from shareholders to creditors. Unreported tests show the (in)sensitivity of the main results vis-à-vis monitoring coefficients obtained after accounting for covenant violations satisfying different combinations of these sample restrictions. Results are available upon request. C. Heterogeneous Effects of Covenant Violations across Banks The RDD specifications described so far do not capture heterogeneity across banks in borrowing firms’ investment changes in the wake of covenant violations. We pursue a two-step approach to augment specification (3) to study bank heterogeneity in terms of capitalization, funding structure, and business models. 7. We estimate specifications with rich sets of fixed effects by means of the Stata package REGHDFE, which implements the estimator proposed by Correia (2016). 8. In our sample, 35.8% of all loans are violated at least once. Of these, roughly 18.5% (or 6.6% of our sample) are violated in all quarters of their lifetime. First, we use the variables defined as above to estimate the RDD specification: Il,b,f,q=𝛼⋅vl,q−1+∑ b ∑ y 𝛽b,y⋅vl,q−1×𝛾b,y (5) +𝜼xf,q−1+𝜻pl,q−1+𝛾b,y +𝛾f+𝛾q+𝛾e+ϵ l,b,f,q. Relative to Equation (3), Equation (5) interacts vl,q−1with bank-year fixed effects (𝛾b,y).9 The parameters of interest are 𝛽b,y, which gauge the time-varying component of bankspecific treatment effects of covenant violations on investment. In the second step, we specify the estimated coefficients  𝛽b,yas the dependent variables to study the relationship between  𝛽b,yand bank funding structure, controlling for bank’s business model traits. The bank-year panel specification to estimate is: (6)  𝛽b,y=𝜓+𝜽𝚪b,y−1+𝜐b,y, where 𝚪b,y−1is a vector of bank characteristics at annual frequency capturing funding structure through the level of equity capital (leverage ratio, risk-adjusted Tier 1 capital ratio) and debt composition (deposits and short-term funding), as well as the bank’s business model through the scope of activities (noninterest income, trading activity, and bank size) and technology and efficiency (nonperforming assets, net income, and cost-to-income ratio) of the bank. All variables in 𝚪b,y−1are measured as of the last quarter of the year and lagged by 1 year. We first estimate univariate regressions for each of the bank characteristics contained in 𝚪b,y−1and then a multivariate regression for the entire vector of covariates. In additional tests, we also interact 𝚪b,y−1 with measures of macroeconomic conditions to investigate how the role of different bank characteristics varies over the business cycle. 9. Ideally, we would interact vl,q−1with bank-quarter fixed effects rather than bank-year fixed effects. Yet small banks experience only very few covenant violations in a specific quarter. This can lead to situations where all covenant violations on loans extended by a small bank in a given quarter are happening for loans that were syndicated together with other, larger banks in our sample. In those cases, it is problematic to disentangle the role of small banks from that of large players in the market. Therefore, we cannot estimate many bank-quarter-specific violation coefficients. To alleviate this issue, we interact vl,q−1with less granular fixed effects at the bank-year level. COLONNELLO, KOETTER & STIEGLITZ: BENIGN NEGLECT OR BLISSFUL BANKING? 465 Whereas the first-step RDD estimates plausibly allow for causal inference on the (bank-timespecific) treatment effect of covenant violations on investment, the second step provides only correlations. As pointed out by Chodorow-Reich and Falato (2018) in a similar setting, to interpret 𝚪b,y−1estimates causally, we would need to have “as good as random” matching between borrowers and banks. Unlike Chodorow-Reich and Falato (2018), we do not focus on the years around the Great Recession to achieve such a condition, thus we are left with arguably nonrandom matching (Schwert 2018). Our solution is to conduct two quasiexperiments within the second-step estimation. To test the implications of bank equity and funding fragility for monitoring intensity, we exploit plausibly exogenous shocks to (a) equity capital resulting from the U.S. banks’ assessment in the SCAP stress test of 2009 and (b) exposure to bank runs following changes in the deposit insurance coverage around the world, respectively. These experiments scrutinize if the baseline correlation analysis between bank monitoring and funding structure supports a causal interpretation. We provide more details in Section C. Two caveats concerning the two-step approach remain. First, whereas we cluster standard errors by bank in Equation (6), the dependent variable  𝛽b,yis generated, which may require further corrections of standard errors because of measurement error (Dumont et al. 2005; Feenstra and Hanson 1999; Gawande 1997). Assuming that the measurement error (  𝛽b,y−𝛽b,y) is uncorrelated with the error term 𝜐b,y, the ordinary least squares (OLS) estimator  𝛉is consistent, but suffers from inflated standard errors, possibly leading to an under-rejection of the null hypothesis of nonsignificance (Roberts and Whited 2013).10 Second, by construction the sample size in the second step is substantially smaller than in the second step, which limits statistical power and may entail an under-rejection of the null hypothesis of nonsignificance. Appendix Section 5 (Supporting information) presents a one-step approach addressing both caveats, which is less flexible although to study bank monitoring behavior. Therefore, we report in the remainder results from the two-step procedure. 10. With a slight abuse of notation, we denote both the OLS estimator and the actual estimate as  𝛽b,y. III. DATA We describe data sources, sample selection, variable construction, and summary statistics. A. Data and Sample Selection Procedure We use data on syndicated loans, borrowing firms, lending banks, and macroeconomic conditions. Syndicated loan data are from the Thomson-Reuters’ Loan Pricing Corporation DealScan (Dealscan) database. We use quarterly accounting and stock price data about U.S. public firms from the Center for Research in Security Prices/Compustat Merged (CCM) database, excluding financial institutions and utilities. We drop firm-quarters with missing information about sales, number of shares outstanding, stock price, and calendar date. We also drop firm-quarters for which net property, plant, and equipment (PPE) is below $1M, for which leverage is zero, or for which the market (book) leverage lies outside of the unit interval. We match them to the syndicated loans using the link file provided by Michael Roberts, which builds on the sample of Chava and Roberts (2008). We use bank quarterly balance sheet data from Compustat Banks, supplemented with Bankscope if information are missing for the 20 most active lenders. Syndicated loan and bank data are combined using the link file made available by Michael Schwert (2018). As a result, we focus on the 103 most active banks on the U.S. syndicated loan market, of which 87 are covered by Compustat Banks. Unlike most of the literature, we sample all syndicate members and not only lead banks. Macroeconomic data are retrieved from the Federal Reserve Economic Data, St. Louis Federal Reserve Bank. The sample starts in 1994, which is the first year when Dealscan provides sufficiently comprehensive information about covenants (Chava and Roberts 2008). The sample runs until 2012, which is the last year covered by the DealscanCCM link file of Michael Roberts. We focus on Dealscan loans containing covenants on (tangible) net worth or the current ratio as in Chava and Roberts (2008) and build a matched quarterly panel of firms, which are assumed to be subject to a given covenant up to the maturity date of the corresponding loan. We identify covenant violations by testing if the observed (tangible) net worth or current ratio complies with the contractual threshold. This approach might result in some false positives, but enables us to measure the distance between the accounting quantity and 466 ECONOMIC INQUIRY the covenant threshold to enhance identification in the RDD. We treat each syndicated loan as a number of separate loans to gauge heterogenous bank behavior, that is, a loan deal of a given borrowing firm with ndifferent banks enters as n separate bank-firm deals. As in Schwert (2018), deal-bank-firm triplets are the panel unit of analysis to study quarterly covenant violations as opposed to firm-quarter level violations in Chava and Roberts (2008). B. Variable Construction and Summary Statistics In our analysis, we rely on borrowing firmlevel and bank-level time-varying characteristics. Concerning borrowing firms’ variables, investment is defined as capital expenditures over last quarter’s PPE. Tobin’s qis defined as total assets minus book equity plus market capitalization scaled by total assets. Cash flow is defined as income before extraordinary items plus depreciation and amortization over last quarter’s PPE. We use the natural logarithm of total assets as a proxy for firm size. Return on assets (ROA) is defined as income before extraordinary items scaled by total assets. To explain variation in monitoring intensity, we employ a host of bank characteristics contained in the vector 𝚪b,y−1of the second-step specification (6).11 The leverage ratio (common equity/assets) and the risk-adjusted Tier 1 capital ratio capture the bank’s level of equity capital. Deposits-to-total assets and short-term fundingto-total assets speak to the composition of its debt. The natural logarithm of total assets (i.e., bank size), noninterest income over total revenue (i.e., the reliance on nontraditional banking services), and assets held for trading scaled by total assets (i.e., the involvement in trading activities) relate to the range of activities the bank operates in. To proxy for the monitoring technology and overall efficiency of the bank, we specify nonperforming assets-to-total assets, net income-tototal assets, and the cost-to-income ratio. Table A.1 (Supporting information) provides the list of 51 banks for which all of these variables are 11. A caveat is the neglect of syndicate loan shares. Studies using publicly available datasets highlight the role of the lead arranger’s loan share (see, e.g., Lee and Mullineaux 2004; Sufi 2007). But administrative data yields mixed evidence on whether the syndicate role (Gustafson, Ivanov, and Meisenzahl 2020) or rather participants’ economic exposure (Plosser and Santos 2016) are key to explaining monitoring intensity. available for at least 1 year and can thus be included in the sample for the second-step estimation. These 51 banks still capture a large fraction of the market, namely 57.3% of all deals extended by our sample banks, calculated on the facility-level as in De Haas and Van Horen (2013) (64.7% of the total credit). Finally, we measure U.S. macroeconomic conditions by using an indicator variable for National Bureau of Economic Research recessions, the National Financial Conditions Index, and the Chicago Fed National Activity Index. Table 1 shows summary statistics for firm variables in and outside covenant violations (panel A and panel B, respectively), bank characteristics (panel C) and selected deal loan characteristics (panel D). Covenant violating firms exhibit lower investment, cash flows, and ROA than other firms. They are also smaller and more levered. On average, the loan syndicates in our sample comprise 5.21 institutions, and 95% of deals include at least one revolver loan, arguably a monitoring intensive credit type. All firm and bank variables are winsorized at the 1st and 99th percentile. All monetary variables are expressed in millions of 2010 dollars. We provide detailed variable definitions in Table A.2 (Supporting information). IV. INVESTMENT AND COVENANT VIOLATIONS As a building block for our subsequent tests on bank heterogeneity, it is important to verify that we obtain the well-known result of a reduction in investment due to covenant violations (Chava and Roberts 2008; Nini, Smith, and Sufi 2012). The use of an RDD relies on the assumption that the running variable (i.e., the accounting ratio regulated by a covenant in our case) cannot be manipulated. This assumption is unlikely to be violated in our setting. As discussed extensively by Chava and Roberts (2008), lending relationships are valuable and firms are reluctant to risk their relationship and general reputation by manipulating their books. Nonetheless, in Figure A.1 (Supporting information) we implement manipulation tests of the running variables based on the smooth local polynomial density estimator of Cattaneo, Jansson, and Ma (2019), who build on the approach of McCrary (2008). Reassuringly, we cannot reject the null hypothesis of no manipulation for any of the three accounting measures (net worth, tangible net worth, and current ratio). All figures clearly suggest that there is no discontinuity around the threshold (of zero relative distance). COLONNELLO, KOETTER & STIEGLITZ: BENIGN NEGLECT OR BLISSFUL BANKING? 473 their choice set due to their relatively low capitalization. Rather than opting for the course of action maximizing borrowing firms’ value, they chose to impose investment restrictions to protect their short-term claim on a borrower’s cash flow. In other words, their action can be seen as an example of excessive monitoring. The idea of excessive monitoring may seem counterintuitive at first sight. As noted by Pagano and Röell (1998), researchers in corporate finance usually think about settings in which principals provide too little monitoring due to free-riding. But from the viewpoint of firm owners, monitoring can be excessive. Specifically, Pagano and Röell (1998) and Burkart, Gromb, and Panunzi (1997) show how shareholders’ overmonitoring can reduce firm value by disincentivizing managers from showing initiative and finding new investment projects. Specific to the case of monitoring by banks, Besanko and Kanatas (1993) and Carletti (2004) illustrate that in certain principal-agent settings banks monitor excessively and maximize utility at the expense of borrowers. Another strand of theoretical literature on inefficient bank interventions investigates financial contracting as a means to alleviate liquidation bias in distress (e.g., Gennaioli and Rossi 2013). Overall, the second-step results clearly support the equity buffer hypothesis. Better capitalized banks are more benign monitors of covenant violating firms. This monitoring style is associated with improved borrower performance, pointing to its efficiency rather than to distraction or shirking of managers and loan officers of wellcapitalized banks. Additional tests show that the bank monitoring measure does not correlate with the state of the business cycle (Figure A.3 and Table A.8 in Supporting information). Likewise, the baseline results on the role of equity and debt structure for monitoring are robust to using a one-step procedure that does not suffer from the econometric issues discussed in Section C (Figure A.4 and Tables A.9–A.11 in Supporting information). C. Quasi-Experimental Evidence We use the 2009 U.S. SCAP stress test to draw causal inference on the equity monitoring hypothesis versus the equity buffer narrative. On May 7, 2009, the Federal Reserve Board (the Board) released the results of its first stress test after the financial crisis (the SCAP) for the 19 largest U.S. banks. Ten banks were identified to have severe capital shortfalls, ranging from $0.6 to $33.9 billion. The results induced 14 banks to issue equity in the 3-month window around the publication of results. Importantly, as noted by Greenlaw et al. (2012) affected banks were not issuing capital in the 3 months before the publication. According to Morgan, Peristiani, and Savino (2014) the size of each bank’s capital shortfall identified in the SCAP was not anticipated by market participants. Thus, we interpret this equity issuance as a plausibly exogenous increase in Tier 1 capital. We use issuance in the 3 months after the publication of the stress test scaled by 2008 total assets as our treatment intensity indicator. Figure 2 shows that there was no clearly discernible difference in terms of Tier 1 capitalization as of the end of 2008 across treated banks (i.e., those that issued equity in the 3 months after the SCAP) and nontreated banks. The Board based its stress test on criteria that were not known ex ante and not tightly linked to Tier 1 capital, which arguably explains why markets did not anticipate the SCAP results. Reassuringly, the treated and nontreated group appear to be heterogeneous in terms of business model, both comprising a mix of global and more regional banks. Table 6 shows the results of a difference-indifference analysis. We interact the SCAP treatment measure indicator with year-indicators for the years 2010, 2011, and 2012 or a cumulative post-period indicator that is equal to one starting in 2010. We also control for bank-level total TARP equity injections scaled by 2007 total assets to account for selection into treatment, as well as for bank characteristics in 𝚪b,y−1. Across a range of specifications involving different sample restrictions and preand post-periods, we find a positive and significant effect of equity issuance activity linked to the SCAP on monitoring intensity. The positive effect of such equity shocks work in the same direction as Tier 1 capital in the baseline correlation analysis and corroborates the equity buffer narrative. Finally, we exploit plausibly exogenous shocks to banks’ exposure to runs, both on the deposit and on the wholesale funding market. Specifically, we specify in the vein of the SCAP analysis above three indicators of funding fragility: exposure to the reform of deposit insurance taken from Lambert, Noth, and Schüwer (2017), substantial co-syndication with Lehman Brothers, and large exposures to the subprime residential mortgage market. Tables 474 ECONOMIC INQUIRY FIGURE 2 Risk-Adjusted Tier 1 Capital Ratio Before the SCAP Stress Test of 2009 Treated banks 0 2 4 6 8 10 12 14 Tier 1 (%) BNYM Bank of America Bb&T Fifth Third JP Morgan Chase KeyBank PNC Regions State Street SunTrust Bank U.S. Bancorp Wells Fargo Non-treated banks 0 2 4 6 8 10 12 14 Tier 1 (%) Associated Bank BBVA Bank of Hawaii Bank of Montreal Barclays Bank CIBC Citigroup Comerica Deutsche Bank HSBC Huntington Lloyds Bank M&I M\&T Bank Northern Trust Nova Scotia RBC RBS SVB Société Générale TD Bank Zions First Note: This figure visualizes risk-adjusted Tier 1 capital ratio for treated (top graph) and nontreated (bottom graph) banks before the SCAP of 2009. The bar charts show the regulatory Tier 1 capital ratio at the end of 2008 together with its minimum threshold of 4% (horizontal blue line). Treated banks are those banks that issued equity in the 3-month window around the SCAP stress test in May 2009. A.12–A.14 (Supporting information) corroborate the absence of evidence that bank funding fragility matters for monitoring. VI. LIMITATIONS This paper is one of the first attempts to empirically quantify how funding structure of banks impacts their monitoring activity. Although covenant violations provide a unique and useful setting to insulate the effect of bank actions on borrowing firms’ governance, our empirical design suffers from some drawbacks on which we elaborate in this section. First, our proxy for bank monitoring may entail nontrivial measurement errors. Besides the issues related to generated variables discussed in Section C and addressed in Appendix Section 5 (Supporting information), covenant violations indeed trigger various bank reactions (such as changes to loan terms) together with enhanced monitoring. Although a dynamic loan renegotiation process is inherent to covenant design and constitutes a form of monitoring by itself (Denis and Wang 2014; Smith 1993), changes in investment due to changes in loan terms should be ideally filtered out. But originations and renegotiations cannot be adequately distinguished in Dealscan (see Roberts 2015), which makes such an exercise difficult. Thus, we have to assume that cross-firm differences in investment adjustment following violations are entirely ascribable to cross-bank differences in monitoring effort. A second issue pertains to selection effects, which relate to contract design at origination as well as to renegotiations of covenants taking place before they are actually breached (Denis and Wang 2014). Controlling for the borrowing firm’s financial policies through a one-step procedure as in Table A.11 (Supporting information) ameliorates this problem. But we cannot rule out that the sample is biased, for example towards those violations entailing smaller costs for borrowers. At the same time, Appendix Section 2 (Supporting information) confirms that the availability of our monitoring measure, which depends on observing enough covenant violations for a COLONNELLO, KOETTER & STIEGLITZ: BENIGN NEGLECT OR BLISSFUL BANKING? 475 TABLE 6 The SCAP Quasi-Experiment  𝜷b,y Dependent Variable (1) (2) (3) (4) (5) (6) (7) 2010 ×Affected (SCAP) 4.110*** (2.79) 2011 ×Affected (SCAP) 3.563** (2.05) 2012 ×Affected (SCAP) 2.586 (0.88) Post (SCAP) 0.077*** 0.055*** 0.045*** 0.020*** 0.041*** 0.006 (5.10) (6.22) (6.30) (2.89) (3.09) (0.57) Post (SCAP) ×Affected (SCAP) 4.313*** 3.718*** 3.425** 3.256*2.597*2.593* (3.09) (3.45) (2.04) (1.90) (1.79) (1.82) TARP −0.021 −0.075 −0.035 −0.042 −0.031 0.391 0.227 (−0.13) (−0.47) (−0.22) (−0.24) (−0.20) (1.38) (0.89) Main interaction terms Yes Yes Yes Yes Yes Yes Yes U.S.-post SCAP interactions Yes Yes Yes Yes No Yes No Bank characteristics Yes Yes Yes Yes Yes Yes Yes Observations 310 269 292 310 236 130 78 Adjusted R20.206 0.153 0.169 0.172 0.132 0.185 0.117 Number of banks 51 51 51 51 37 34 22 Mean dep. var. 0.008 0.005 0.007 0.008 0.006 0.019 0.018 Mean Affected (SCAP) 0.003 0.003 0.003 0.003 0.004 0.003 0.004 Number of treated banks 12 12 12 12 12 11 11 Clustering Bank Bank Bank Bank Bank Bank Bank Sample selection All banks All banks All banks All banks U.S.-banks All banks U.S.-banks Sample period 1994–2012 1994–2010 1994–2011 1994–2012 1994–2012 2007–2012 2007–2012 Note: This table reports estimates from the second-step OLS specification (6) augmented with a difference-in-differences exercise based on the publication of SCAP stress test results on May 7, 2009. The dependent variable is our bank monitoring measure  𝛽b,y. 𝛽b,yis the estimated coefficient from the first-step specification and captures the bank-time specific effect of covenant violations on the borrowing firm’s investment policy. Explanatory variables include Affected (SCAP) (defined as the bank-specific equity issuance after the publication of SCAP results scaled by 2008 total assets) and its interactions with year-specific or cumulative post period indicators for the treatment period, TARP (defined as total TARP take-up scaled by 2007 total assets), and lagged time-varying bank characteristics 𝚪b,y−1. Information on the sample period/selection and standard error clustering is indicated below. Specifications including also non-U.S. banks control for a U.S. bank indicator and its interactions with postSCAP indicators. The tstatistics are reported in parentheses. Significance at the 10%, 5%, and 1% level is indicated by *, **, and ***, respectively. Refer to Table A.2 (Supporting information) for variable definitions. given firm-bank-year triplet, depends on bank characteristics. The latter may also determine the type and the strictness of the covenants negotiated at origination. Third, two important innovations in loan origination became established over the time span of our sample: nonbank lending and covenant-lite loans. Chernenko, Erel, and Prilmeier (2019) show that nonbank lenders rely less on financial covenants. Biswas, Ozkan, and Yin (2019) confirm this finding, but also document that nonbank lenders make extensive use of covenants restricting capital expenditures. By contrast, the rise in covenant-lite term loans did apparently not induce a major shift in covenant design, as banks continue to impose traditional covenants in loan packages through credit line facilities (Berlin, Nini, and Yu 2020). Nonetheless, both nonbank lending and covenant lites are arguably important for our setting. Alas, Becker and Ivashina (2016) note that the reporting quality for the cov-lite indicator in Dealscan is poor and the differentiation between maintenance-based covenants (cov-heavy) and incurrence-based (cov-light) is hindered by several intermediate cases. We believe that all three issues are of relevance. However, the robustness tests that can be conducted given the available data bear only limited indication that they are of first-order importance to the qualitative inference that better capitalized banks take a more lenient monitoring stance. At the same time, future research to scrutinize the sensitivity of this main result based 476 ECONOMIC INQUIRY on more detailed data in a more rigorous fashion seems warranted. VII. CONCLUSION Loan monitoring is a key activity of banks as informed lenders. Several theories link the intensity and effectiveness of such an activity to bank funding structure as well as to the state of the business cycle. This paper studies heterogeneity in monitoring across banks in the context of syndicated loans to U.S. firms. Making use of a granular data structure linking lending banks to borrowing firms, we extract a bank-time specific measure of monitoring intensity. More specifically, we measure monitoring by analyzing banks’ interventions in borrowers’ management after covenant violations, which we approximate by firms’ changes in investment policy. This monitoring measure reveals the existence of substantial heterogeneity in monitoring both across banks and over time. The results clearly indicate that equity capital is an important determinant of bank monitoring incentives. Well-capitalized banks, which are better able to absorb negative shocks on their loan portfolio, keep a looser stance towards borrowing firms. This looser stance is linked to improved borrowers’ performance instead of being distortive. 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