Does mandatory IFRS adoption facilitate debt financing?

Over 2000–2011 the total amount of private credit and outstanding corporate bonds in the EU was 193 % (as a percentage of GDP), whereas the total value of all shares listed on European stock markets was 59 %. Similarly, the total amount of U.S. corporate debt (both loans and bonds) over the same period was 323 % as opposed to the total market capitalization of stocks which was 126 % (for further details see World Bank, Global Financial Development Database).

Similarly to Ball et al. (2014), Kim et al. (2011) focus on bank loan contracts and examine the impact of voluntary adoption of International Accounting Standards (IAS) on various aspects of the terms of private debt agreements. Chen et al. (2013) examine the debt market effects of mandatory IFRS adoption, again in the context of bank loan contracts. Finally, Beneish et al. (2012) examine the macroeconomic debt effects of mandatory IFRS adoption by focusing on country-level foreign debt investment.

Ball et al. (2013) also study the implications of the contracting differences between public and private debt lenders, but they focus solely on U.S. cross-listings. Consistent with the bonding hypothesis, which predicts debt market benefits because of stronger creditor protection and legal enforcement in the United States, they demonstrate that cross-listed firms are more likely to raise public debt and also to incur lower yield spreads but only for bonds.

In this respect, Ahmed et al. (2013) investigate mandatory IFRS adoption and document less timely loss recognition.

IAS 40 requires that the fair value of an investment property asset is either recognized on the balance sheet or disclosed in financial statement footnotes.

Muller et al. (2011) focus on European real estate firms. They find larger declines in information asymmetry in the post-IFRS period, as reflected in lower bid-ask spreads, for mandatory IFRS adoption firms that did not provide fair values before adoption. However, they also show that these firms continue to have higher information asymmetries than voluntary adoption firms, which appears partly attributable to the generally lower reliability of fair values. Similarly, Christensen and Nikolaev (2013) study the accounting treatment of long-term nonfinancial assets by mandatory IFRS adopters in the United Kingdom and Germany. They document that fair value accounting is used exclusively for property, most likely because of the relative liquidity of property markets, which therefore provide more reliable measures of fair value. They also show that firms that report reliable fair value estimates of investment property tend to access the debt markets more frequently.

The number of observations is slightly lower than the total number of issues of 14,003 reported in Table 1. This is because of lost observations when the independent dummy variables (i.e., the industry-year or country indicators) perfectly predict the dependent dummy variable.

We re-estimate Eq. (1) using a double-censored (i.e., two-limit) tobit, given that the dependent variable Public Market Continuous has a lower value of 0 and an upper value of 1. Alternatively, we also apply a logit transformation of the dependent variable. In both cases, results remain qualitatively identical.

Although we focus on mandatory IFRS adopters, note that prior literature documents different dynamics for voluntary adopters than for first-time adopters of capital market changes at the time of the IFRS mandate. This implies how complex these dynamics are for voluntary adopters. For example, Florou and Pope (2012) report different quarterly incremental institutional holding changes around mandatory IFRS adoption between voluntary and first-time adopters. Similarly, Daske et al. (2008) find a larger decline in the cost of equity for voluntary than first-time adopters when IFRS financial reporting becomes mandatory. Li (2010), in contrast, does not document any change in the cost of equity for voluntary adopters around mandatory IFRS adoption.

Term Spread is calculated as the difference between the 10- and two-year government bond rate at the country-month level. We obtain data on monthly government bond rates from Datastream. Median DTD is the country-month median value of the firm-level distance to default (DTD) measure that combines leverage and asset volatility. The firm DTD measures come from the Risk Management Institute (RMI) at the National University of Singapore (NUS). For more details, see www.​rmicri.​org, and Duan and Wang (2012). The firm-level DTD measure is not available for all our sample firms. Nevertheless, in our primary analysis, we also estimate the cost of debt model after including the firm-level DTD.

Our main findings remain robust to the inclusion of separate fixed effects by year and by industry as well as to the inclusion of firm-level fixed effects.

We employ one-way clustering at country-year level (i.e., our clustering unit is every year in a given country). We assess the sensitivity of our primary analysis to two-way clustering by country and by year and find that our results persist. However, we note that given our relatively short period (eight year clusters) and the number of our country clusters that can be as low as 13 (depending on the estimated model), two-way clustering by country and by year can be subject to the “small cluster” problem and lead to biased standard errors (Petersen 2009, p. 460).

Note that 26 % of total Dealscan observations have a ticker symbol; this percentage is lower than the 43 % reported by Dichev and Skinner (2002). However, their study is based only on U.S. loans. If we focus only on U.S. private issues, we also find that 42 % of the total Dealscan population has a ticker symbol.

To the extent that it is less appropriate to compare long-term public debt with private shorter-maturity debt, we assess the sensitivity of our findings to the exclusion of 364-day facilities, which account for 15.3 % of total loans in our sample. Our results remain qualitatively unchanged.

Nevertheless, we assess the robustness of our analysis to potential selection biases and find qualitatively identical results (see Sect. 4.4). Also, prior research suggests that some loans covered by Dealscan are renegotiations of existing deals, rather than new deals. Identifying renegotiations is not possible based on the information provided by Dealscan. It would also require manual data collection, which is not feasible because of weak national reporting requirements (Roberts and Sufi 2009). Arguably, a lender who renegotiates with a firm already has private information and is less reliant on the firm’s financial statements than a first-time lender would be. However, while the level of dependence on financial statements may vary across private lender types, prior theory predicts that all banks have access to private information and therefore rely less on public financial statements than bond holders (see Sect. 2). We believe our inferences regarding the debt-market effects around mandatory IFRS adoption are unlikely to be biased because of renegotiations.

We also assess the robustness of our findings to the use of country- and industry-adjusted control variables. Our results remain qualitatively identical to those reported.

We further analyze this result by investigating the comparability explanation based on the approach of Daske et al. (2008). Specifically, we generate a new variable %Voluntary Adopters, defined as the proportion of firms voluntarily reporting under IFRS in a given industry, transformed into a binary indicator based on the industry median of %Voluntary Adopters within the treatment sample. Next we interact this indicator with all IFRS indicators. If many industry peers already report under IFRS by the mandatory adoption date, then voluntary adopters should experience fewer positive externalities from the IFRS mandate. Similarly, one would expect mandatory adopters to benefit more when there are already many peers reporting under IFRS. In our regression analysis (untabulated), we find that in both cases (i.e., Voluntary*Mandatory and First-Time Mandatory) the coefficient estimate on the interaction term with %Voluntary Adopters has the predicted sign (i.e., negative and positive respectively) but is insignificant under all specifications. Therefore we cannot provide strong evidence supporting the notion of comparability effects. Also, the coefficient on Voluntary is negative and significant under all specifications, although this result does not always persist when using a constant sample of firms (see panel B) or when performing sensitivity tests (see Table 7, panels C and F). In general, we note that results regarding voluntary IFRS adopters should be interpreted cautiously for at least two reasons: (a) our research methodology may not be ideal for examining the debt market implications of voluntary IFRS reporting, given that the focus of our study is mandatory IFRS adoption (e.g., in line with prior related literature, we exclude voluntary adopters from our benchmark sample countries); and (b) there are potential problems of self-selection bias (Li 2010; Kim et al. 2011; Kim and Shi 2012).

Based on 10 % of international debt issues during 2001–2010 having at least one recorded covenant Ball et al. (2014) document a significant decline in accounting-based covenants for mandatory IFRS adopters following adoption; this decline is larger for loans than bonds. We highlight here that the enhanced information environment of mandatory IFRS adopters is the main channel through which borrowers can circumvent the higher agency costs in the public debt market and are therefore more likely to issue a bond (as opposed to borrow privately). An alternative explanation is that this shift from private to public debt can be attributed to the IFRS-related reduction in the use of accounting covenants for loans and therefore less efficient loan contracting; however, this is less likely given that private lenders can use alternative agency cost mitigating mechanisms (e.g., maturity, collateral) to compensate for the increased monitoring costs. We thank an anonymous referee for this insightful comment.

While it is not possible to directly compare our samples due to different research design choices (e.g., different sample periods), we note that Chen et al. (2013) employ a nonconstant sample of 21,487 loans with loan spread data over 2000–2009 (see their Table 5, panel C). However, we are puzzled by the sample size of Chen et al. (2013), given that it is considerably larger than those employed in prior studies using the same database, including ours (e.g., Qian and Strahan 2007, see their Table III; Bharath et al. 2008, see their Table 5; Kim et al. 2011, see their Table 4; Ball et al. 2013, see their Table 4).

Our insignificant coefficient estimate on Voluntary under the loan specification contrasts with the findings of Kim et al. (2011), who examine the loan contracting implications of voluntary IFRS reporting and document significantly lower loan rates for voluntary adopters. As mentioned earlier in footnote 18, results on voluntary adopters should be interpreted cautiously. These results are not directly comparable to those of Kim et al. (2011), who focus on voluntary rather than mandatory IFRS reporting and therefore adopt a different research design. For example, our sample differs from that of Kim et al. (2011) in its periods, composition and number of sample countries, exclusion of voluntary adopters from benchmark sample countries, etc. Nevertheless, we replicate their analysis using our sample countries over 2000–2005 after (a) including voluntary adopters in the benchmark countries, (b) excluding the United States, and (c) considering the potential endogeneity of voluntary IFRS adoption. Specifically, following Kim et al. (2011) and Kim and Shi (2012), we employ a Heckman’s (1979) two-stage approach. In the first stage, we estimate a probit IFRS adoption model in which the likelihood of IFRS adoption is regressed on a set of firm-specific variables predicted to influence the demand for IFRS reporting namely size, leverage, earnings growth, percentage of foreign sales to total sales, and cross-listing on foreign exchanges (as well as country-, industry- and year- fixed effects). In the second stage, we estimate our loan spread specification (i.e., our Eq. 2) after including the inverse Mills ratio estimated from the above first-stage regression. In line with Kim et al. (2011), we find that the cost of loans decreases significantly by almost 28 basis points for voluntary adopters (t-stat = 2.17). However, similarly to Kim et al. (2011) and Kim and Shi (2012), we acknowledge the potential limitations of the instrumental variable approach.

As noted earlier, Ball et al. (2014) document a significant decline in accounting-based covenants for mandatory IFRS adopters following adoption, primarily for loans. Moreover, they document a substitution of accounting with non-accounting covenants consistent with IFRS adoption reducing the effectiveness of accounting covenants but only for loans; no such substitution effect is observed in bond contracts. This observation combined with the paucity of accounting covenants in public debt suggests that our documented IFRS-induced decline in the cost of bonds cannot be associated with any IFRS-related changes in accounting covenants used in bonds. Indeed, following (Ball et al. 2014), we identify only 40 public debt issues (i.e., 0.69 % of total bonds used in the cost of debt analysis) that have at least one accounting covenant.

The only exception to the above is Model 2, where both estimates of First-Time Mandatory _{Low_Gaapdiff} and First-Time Mandatory _{High_Gaapdiff} are significantly positive (0.240 and 0.406, respectively) and the difference between the two estimates is statistically insignificant (p value of χ ²-statistic = 0.351).

However, in their discussion paper, Barth and Israeli (2013) argue that both IFRS reporting and enforcement changes are necessary to confer the benefits documented by Christensen et al. (2013).

The coefficient on First-Time Mandatory _{EU_ENF} is also significantly positive under all models in the access to debt analysis; the difference in the coefficient estimates between the two groups of countries (i.e., European Union with and without enforcement changes) is always statistically insignificant. Moreover, the coefficient on First-Time Mandatory _{EU_ENF} is negative but insignificant under the cost of bonds specification, suggesting that first-time IFRS adopters from countries with financial-reporting-enforcement changes do not experience a decline in the cost of public debt. A plausible explanation could be that two out of four countries with enforcement changes included in this model (i.e., Netherlands and the United Kingdom) are classified as low Gaapdiff, which do not experience any IFRS-related changes in the cost of bonds (see panels A and B).

We thank Kim et al. (2012) for kindly providing us with these scores.

Contrary to debt-market effects, equity-market changes associated with mandatory IFRS financial reporting are confined to countries with strong enforcement regimes (see the review by Brugemann et al. 2013). While we have no strong prior regarding the differential role of enforcement between the equity and debt markets, one possible explanation is that debt-contracting terms substitute for poor country-level creditor-protection mechanisms. For example, using a cross-country sample of Yankee bond contracts, Miller and Reisel (2012) document more restrictive covenants attached to corporate bonds when the country’s creditor rights laws are weaker, financial disclosure laws are less stringent, and laws on fines and penalties are more lenient.

In particular, first we employ a sample of issuers with at least one observation before and after mandatory IFRS adoption (i.e., our constant sample of firms). Then, following prior literature (e.g., Barth et al. 2012), we match each issuing firm-year of the treatment sample in the pre-IFRS period with one of the benchmark sample in the same period by industry sector and size. We measure size by total assets and keep the closest possible benchmark firm-year. The matching is done separately for the access to debt and cost of debt samples. In our empirical analysis, we use only debt issued by firm-years that have matches (note that we match all issues by treatment firms). Untabulated tests show that differences in the mean values of many variables (e.g., size, tangibility, current ratio, returns variability, etc.) between treatment sample firms and matched control issuers are insignificant, suggesting that, in general, out treatment and matched benchmark samples are similar.

We thank the editor and an anonymous referee for raising this point.

In fact, Armstrong et al. (2010) mention that in their review of the accounting, finance, and economics journals over the past 20 years, they could not locate any papers that examine whether attributes of the firm’s financial reports influence their ability to access the debt markets.

Findings are robust to the inclusion of nondebt tax shields (Giannetti 2003) and the use of firm fixed effects (Faulkender and Petersen 2006) in the leverage model and after controlling for the propensity of a firm to issue a loan in the same year in the access to debt models (Ball et al. 2013). However, we note that these results should be interpreted with caution; from an empirical perspective, it may be less appropriate to classify firms not included in our sample (i.e., firms that are likely to be debt active but are not covered by SDC or Dealscan) as not making use of public debt (i.e., as having the dependent variable equal to zero). In other words, the lack of debt data for these firms does not necessarily imply that they do not actually issue a bond. Moreover, setting the dependent variable constantly equal to zero does not capture the change in the issuing behavior of these firms across public and private debt markets around the time of IFRS adoption.

We find that, in the first stage regressions, the coefficient estimates of all instruments have the predicted sign and are statistically significant. To test the relevance of instrumental variables, we also report the Kleibergen-Paap Wald F-statistic as a test of weak identification in the context of clustered standard errors, and the Hansen’s J-statistic as a test of overidentification for loans where we have more instruments than endogenous variables. Under the first test, we obtain a 51.389 test statistic value for bonds, and a 46.407 value for loans. For both cases, the F-statistic exceeds the critical values of 16.38 and 13.43, respectively, indicating the instruments are not weak. Under the second test, we obtain a 1.738 test statistic value (p value = 0.187) for loans, indicating that the instruments are valid. However, we note that finding good instruments in accounting research can be very challenging (see, e.g., Larcker and Rusticus 2010; Roberts and Whited 2013). The construction of all variables is described in the “Appendix”.