RDP 2022-05: The Real Effects of Debt Covenants: Evidence from Australia 3. Direct Effects of Covenants

In this section I explore the direct effects of debt covenants on real business activity and aim to disentangle the mechanisms. As discussed above, the direct effects of debt covenants can stem from the ‘ex post punishing channel’ following a breach or the ‘ex ante disciplining channel’ in the absence of any breach. The latter happens when firms try to manage their activity and financial position to avoid breaching covenants. Figure 4 (top panel) plots the density of the interest coverage ratio by firms subject to ICC in the data, showing a significant bunching right before 2, which is a common minimum critical threshold. By contrast, there is no significant evidence of manipulation of the ratio by firms subject to other types of covenants but not ICC (bottom panel). This suggests that firms try to avoid breaching ICC and, as such, supports the disciplining role of debt covenants.

To examine the overall direct effects of debt covenants, I first estimate the following baseline empirical model:

(1) $Δ y i,t = α i 0 + β 0 Co v i,t−1 + X ′ i,t−1 μ 0 + ∑ s θ s 0 I i,s t+ ε i,t$

The dependent variable $\text{Δ}{y}_{i,t}$ represents real business activity of firm i in year t. For investment, it is measured by the log difference in fixed assets (property, plant, equipment and machinery) between t and t–1. For employment, it is measured by the log difference in staff and employees expenses. Covi,t–1 indicates whether firm i was subject to debt covenants in time t–1. The parameter of interest ${\beta }^{0}$ traces the relationship between the firm's real business activity in period t and its exposure to covenants in period t–1. The random error term ${\epsilon }_{i,t}$ is allowed to be correlated within firm observations and potentially heteroskedastic with the standard errors being clustered at the firm level.

The simple reduced-form approach faces several empirical challenges. First, there is a potential reverse causality issue; that is, business activity causes exposure to debt covenants. On one hand, firms and creditors may anticipate a future drop in business activity and insure against that by incorporating debt covenants, contributing to a negative correlation between outcomes and covenants. On the other hand, firms could have hiring and investing strategies that lead to extra borrowing and, in turn, the covenants associated with the loan facilities. Similarly, firms may try to reduce expenses prior to loan applications and return to normal activity subsequently. In the latter two cases, the reverse causality should work against finding a negative link between business activity and exposure to covenants.

To address these potential endogeneity issues, I include the vector of covariates ${{X}^{\prime }}_{i,t-1}$ to control for time-varying firm-level financial measures such as the usual proxies for firm size (total assets), performance (total revenue), credit (debt), financial structure (gearing ratio) and liquidity (cash holding). Inclusion of firm fixed effects, ${\alpha }_{i}^{0}$ controls for the unobserved time-invariant firm-level components (e.g. its origin and mission, managerial abilities and risk preferences, as well as sector and associated sector-level characteristics that do not vary over time). To the extent that the observed firm-level time-varying financial measures and firm-specific fixed effects inform the firm and creditors about its future conditions, this helps reduce potential reverse causality bias. These firm-level controls also help address the potential selection bias in the reporting of debt covenants by firms' characteristics as discussed in Section 2.

Lastly, both the actual usage and the reporting of debt covenants may change over time due to changes in aggregate economic and credit conditions, such as the tightening in credit availability and financial regulations during and following the global financial crisis, as well as changes in financial reporting standards. As these factors are likely to vary across industries, I include the sector-level time trends Ii,st where Ii,s indicates the sector s of firm i. Even with all these controls, it is important to emphasise that identification relies on the underlying assumption that exposure to debt covenants does not coincide with firm-level temporary shocks that are not captured by the controls.

As an alternative to unpack the channels of the direct effects, I employ an empirical strategy similar in spirit to a difference-in-differences framework. I first focus on firms that were not recently exposed to nor breaching any covenants. More specifically, I estimate the following equation:

(2) $Δ y i,t = α i 0 + β 1 Di s i,t−1 + X ′ i,t−1 μ 1 + ∑ s θ s 1 I i,s t+ ε i,t$

where

That is, the ex ante effect of debt covenants is identified by comparing the control group (not previously nor currently exposed to debt covenants) with the treatment group (not previously but currently exposed to debt covenants with no breaches). The additional condition that no covenant has been violated in period t–1 eliminates confounding effects of a breach and allows for an effective evaluation of the marginal effects of debt covenants as a disciplinary device. Figure 5 shows that both the control and treatment groups follow parallel and stable trends in investment and employment prior to the treatment group being exposed to covenants (before t–1). Moreover, there are no discernible differential trends in their financial statistics both before and after the exposure treatment (Figure C1). Formal testing of the difference between the time trend coefficients suggests that the time trends in investment and employment before the exposure shock are statistically similar between the two groups, confirming that they are otherwise comparable (Table C1).

Similarly, I attempt to pin down the ex post effect by comparing the control group (previously and currently exposed to debt covenants but no breaches) with the treatment group (previously and currently exposed to debt covenants with current breaches only) as follows:

(3) $Δ y i,t = α i 2 + β 2 Pu n i,t−1 + X ′ i,t−1 μ 2 + ∑ s θ s 2 I i,s t+ ε i,t$

where

However, unlike what's observed for ex ante treatment, trends in investment, and to a lesser degree employment, prior to the ex post treatment vary significantly between control group and treatment group (Figure 6). Moreover, firms' financial statistics experience noticeable deterioration around the breach with an even larger deviation by firms who could not survive following a breach (Figure C2).

Turning to the empirical results, Table 2 presents the estimates of relevant coefficients in Equations (1), (2), and (3) for investment and employment. All specifications include the full set of firm-level controls, firm fixed effects and sector-level time trends. The first column shows that, overall, being subject to covenants is associated with a more than 11 per cent drop in investment and more than 6 per cent drop in staff expenses. That is equivalent to $50 million in investment and$3 million in staff expenses, on average. Equation (2) isolates the ex ante disciplining mechanism and shows that the exposure treatment is associated with an 11 per cent drop in investment and a 9 per cent drop in staff expenses. By contrast, estimates of the ex post effect are not particularly significant, which is unsurprising given the differing trends prior to the covenant violation (Figure 6). Overall, these results suggest the importance of debt covenants as an ex ante disciplining device, over and beyond the effects of their violations.

Table 2: Direct Effects of Debt Covenants on Investment and Employment
Overall and across different channels
Equation (1)
Overall $\left({\beta }^{0}\right)$
Equation (2)
Ex ante $\left({\beta }^{1}\right)$
Equation (3)
Ex post $\left({\beta }^{2}\right)$
Investment −0.114***
(0.037)
−0.118**
(0.055)
0.021
(0.132)
Observations 5,577 2,966 1,120
Staff expenses −0.065***
(0.024)
−0.092*
(0.050)
−0.095*
(0.057)
Observations 4,007 2,069 846
Firm fixed effects Yes Yes Yes
Financial measures Yes Yes Yes
Sector time trends Yes Yes Yes

Notes: Clustered standard errors at firm level are shown in parentheses. ***, ** and * denote statistical significance at the 1, 5 and 10 per cent levels, respectively.

Sources: Author's calculations; Connect4; Morningstar

To ensure that the estimates are not driven by mining firms with large investment and very low likelihood of being exposed to covenants, I estimate all three equations on non-mining firms and find that the ex ante effects of debt covenants appear even stronger on non-mining investment. As seen in Section 2, firms subject to covenants are substantially larger than those not subject to covenants. To check the results against potential underlying factors associated with smaller firms that are not captured by their financial statistics, I also estimate the models using a sample of larger firms only. They are defined as having annual revenue greater than $2 million before 2015 and$10 million after 2015. The estimates are broadly similar to the full sample. Finally, there may be underlying factors that lead to firms never engaging in debt covenants. I address this concern by removing firms not subject to covenants throughout their lifespan in the sample. Results suggest much stronger direct effects of debt covenants, particularly through the disciplining channel. All robustness checks can be found in Appendix D.