Analysts’ Earnings Adjustments and Changes in Accounting Standards
Frank Ecker
Duke University
Tomas Hjelström
Stockholm School of Economics
Per Olsson
ESMT European School of Management and Technology
Hanna Setterberg
Stockholm School of Economics
February 2016
Abstract: We investigate how financial analysts’ processing of earnings information is affected by changes in
accounting standards; specifically, we measure the extent to which analysts make adjustments to earnings before and
after European firms’ transition to International Financial Reporting Standards (IFRS). We further document how
the magnitude of analysts’ adjustments has properties consistent with notions of earnings quality. We find a marked
decrease in the absolute level of earnings adjustments following IFRS transition, both for mandatory adopters (in
2005) and voluntary early adopters (in varying prior years). The number of adjustments also decreases. The IFRS
transition effect is larger in countries with stronger legal enforcement and countries whose domestic accounting
standards were more dissimilar to IFRS, although the main IFRS effect is not contingent on these factors. Results
are not driven by financial reports being more mechanically comparable after the introduction of IFRS.
We thank Richard Barker, Bo Becker, Katherine Schipper and Martin Walker for their helpful comments and suggestions as well
as conference and workshop participants at Bocconi University, Duke University, KU Leuven, Stockholm School of Economics,
the European Accounting Association Annual Congress 2015, the Nordic Accounting Conference 2014, and the Swedish Society
of Financial Analysts.
Analysts’ Earnings Adjustments and Changes in Accounting Standards
1.
Introduction
In this study we investigate how analyst behavior is systematically affected by changes in
accounting standards. Specifically, we examine the extent to which financial analysts make
adjustments to reported earnings before and after firms’ transitions from various sets of domestic
standards to International Financial Reporting Standards (IFRS). Furthermore, we document
how the magnitude of analysts’ adjustments has properties consistent with notions of earnings
quality, supporting an interpretation of such adjustments as a measure of analysts’ perception of
a firm’s earnings quality (larger adjustments correspond to poorer quality of reported earnings).
Analysts are sophisticated users of accounting information, and how they process earnings
information under different sets of accounting standards is important to understand, especially
when evaluating shifts in accounting regimes.
In addition, the consequences of the IFRS
adoption on earnings quality and other outcome measures is still (sometimes hotly) debated. We
believe an investigation of the quality of reported earnings under IFRS versus domestic GAAPs
from the perspective of financial analysts can inform (but not settle) the debate.
We use the absolute magnitude of analysts’ earnings adjustments as a summary (inverse)
indicator of how they perceive the quality of reported earnings. We argue that analysts will
make larger (or more) adjustments if they perceive the quality of reported earnings to be poor,
i.e., the total magnitude of adjustments is a result of multiple decisions made by analysts about
whether to include or exclude a given earnings component. Prior research has not, to our
knowledge, explicitly linked analyst adjustments to earnings quality. We believe, however, that
evidence in the analyst literature supports associating analyst adjustments with several quality
1
dimensions; that is, we view analyst adjustments as a summary measure of earnings quality as
perceived by financial analysts.1
There is a large empirical literature on adjusted earnings, primarily based on US samples,
often referred to as pro-forma earnings, street earnings, core earnings, or non-GAAP earnings
(e.g., Bradshaw and Sloan 2002, Bhattacharya et al. 2003, Doyle et al. 2003, Lougee and
Marquardt 2004, Gu and Chen 2004, Choi et al. 2007, Heflin and Hsu 2008, Kolev et al. 2008,
Christensen et al. 2011, Doyle et al. 2013, Heflin et al. 2015). The difference between firms’
reported (bottom-line) earnings and analysts’ non-GAAP earnings are the adjustments. In most
cases the adjustments to reported earnings are exclusions (as opposed to additions) of income or
expense items. Many prior studies use the analyst-adjusted earnings number as a proxy for the
firm’s own non-GAAP earnings disclosures (see Bradshaw 2011 for a discussion). In contrast,
we are interested in analyst adjustments per se as an indicator of how sophisticated users of
financial reports perceive reported earnings under different sets of accounting standards.
A second strand of related research pertains to the effects of IFRS adoption on earnings
properties (such as persistence, conservatism and smoothness), capital market outcomes (such as
liquidity measures and returns and volume reactions to earnings announcements), and analyst
outcomes (such as forecast errors and forecast dispersion).2 Results vary, with differences in
findings ascribed to differences in specifications and proxy variables, to differences between
1
For example, analyst-adjusted earnings generally exclude items that are transitory or believed to be of low value
relevance for other reasons (First Call 1999, Gu and Chen 2004), and permanent earnings and high value relevance
are considered key dimensions of earnings quality in the literature (Dechow et al. 2010). In addition, interview and
survey studies on analysts point to an improvement in earnings quality along a number of quality dimensions as
motivation for these adjustments (e.g., Graham et al. 2002, Barker and Imam 2008, Hjelstrom et al. 2014). Archival
studies on US data also show that investors react more to analyst-adjusted earnings than to firms’ reported earnings
(e.g., Bradshaw and Sloan 2002). We discuss this link in more detail in Section 2.1 and test it empirically in Section
5.2.
2
Forecast errors and forecast dispersion are measured at the adjusted (non-GAAP/non-IFRS) earnings level.
Consequently, these studies are not designed to inform about reported domestic GAAP or IFRS earnings, and are
thus conceptually distinct from our study. As reported in Section 5.1, forecast errors and forecast dispersion are also
empirically distinct from earnings adjustments.
2
mandatory and voluntary IFRS adopters (the latter are often assumed to have stronger capital
market incentives), to variation in enforcement, to differences or similarities between domestic
accounting standards and IFRS, and to sample differences.3
In our main tests, we first study analyst-followed firms in European countries that
mandated the transition to IFRS in 2005.4 The explicit motivation for the regulation requiring
firms in these countries to report under IFRS was to improve external financial reporting along a
number of earnings quality dimensions.5 The sample period is 1999 to 2012 and the sample
includes 16,748 firm-years for 1,744 unique firms. Sample firms are required to have domestic
GAAP accounting data before and IFRS data after the transition. Following the literature on
non-GAAP earnings in US samples, we define analyst adjustments as the difference between
reported earnings and the so-called “IBES actual earnings”.6 We document a marked decrease in
the absolute level of adjustments following the IFRS transition across multiple test
specifications. For example, in a test with firm-fixed effects and controls for general economic
conditions and the general time trend in adjustments (as documented by prior research), absolute
adjustments decrease by about 43 % from the pre-IFRS level (significant at the .001 level).
3
For example, Ahmed et al. (2013) conclude that earnings under IFRS are of lower quality than under domestic
GAAP for firms from twenty countries. Barth et al. (2008) conclude the opposite, namely that IFRS adoption leads
to better earnings quality. Atwood et al. (2011) conclude that there are no quality effects. Yip and Young (2012)
find that mandatory IFRS adoption improves comparability, whereas Cascino and Gassen (2015) conclude that any
improvement in comparability is marginal at best. Christensen et al. (2013) conclude that IFRS adoption in and of
itself does not lead to improved market liquidity, whereas Barth and Israeli (2013) argue that one cannot draw such
inferences from the Christensen et al. analysis. Horton et al. (2013) summarize the literature on IFRS adoption
effects on analyst forecast errors and/or forecast dispersion, similarly noting discrepancies in findings.
4
We concentrate on these European countries because we believe the product markets and, albeit to a somewhat
lesser extent, capital markets were relatively integrated. To the extent that analysts’ work is influenced by such
market characteristics we hold them constant through this design choice.
5
The IFRS regulation passed the European Parliament and the European Council in 2002 (European Commission
regulation No. 1606/2002). Article 3 of the regulation states that a common set of accounting standards should be
adopted if “[…] they meet the criteria of understandability, relevance, reliability and comparability required of the
financial information needed for making economic decisions and assessing the stewardship of management.”
6
As explained in more detail in Section 2, IBES actual earnings are earnings after analysts’ adjustments to the
firm’s reported earnings.
3
We next consider a separate sample of firms that voluntarily adopted IFRS prior to 2005,
where the (firm-specific) year of adoption is the event year. This allows us to address the
potential concern that a confounding event in 2005 caused the decrease in adjustments for
mandatory adopters.
Specifically, any confounding event in 2005 should affect all firms,
including those that had voluntarily adopted IFRS in prior years. Results show that there is no
2005 effect on analyst adjustments for voluntary adopters. In addition, the magnitude of the
IFRS effect (in prior years) for voluntary adopters is indistinguishable from the IFRS effect
among mandatory adopters. To further probe the influence of potential confounding events we
directly investigate the issue within the main mandatory adopter sample. Specifically, we
perform a difference-in-difference analysis with a matched US sample as a control group.
Results indicate that there is no universal effect in analysts’ earnings adjustments around 2005
(the adjustment effect is economically and statistically significant for IFRS adopters, and there is
no 2005 effect for US firms).
As is generally the case for analyst adjustment research, we are able to directly observe
only the net amount of adjustments, not the individual adjustments.7 To address this issue we
develop a statistical approach to approximate the number of adjustments by firm and year.
Through an iterative procedure, described in detail in Section 4.4, we identify the combination of
line items (from a set of 20 pre-selected candidates) whose sum is closest to the total adjustment
amount. The average (median) number of line items adjusted for by analysts is 3.36 (3), and
ranges from 1 to 11.8 We believe the analysis provides the first large-sample evidence, at least in
an international setting, of what line items analysts adjust for (because it is a statistical approach,
7
Gu and Chen (2004) provide an exception. They investigate a smaller sample of firms with information on
specific inclusions and exclusions from First Call’s Footnote file.
8
The most frequently excluded items in our sample are special items, gains and losses from the sale of PPE and
investments, and foreign exchange income.
4
however, it may contain non-trivial measurement error).9 We re-estimate our main IFRS test
replacing the magnitude of the adjustments with the number of adjustments as the dependent
variable. Results are consistent with our main findings.
The rest of the empirical analyses concern various validity and robustness tests.
As
discussed in more detail in Section 5.1, (absolute) analyst forecast errors and forecast dispersion
are measured at the adjusted earnings level and thus do not inform about reported earnings per
se. In fact, if analysts are effective in achieving their preferred adjusted earnings number
(regardless of accounting regime), forecast errors and dispersion will not be informative about
differential properties of reported earnings since the adjustment process dampens or even cancels
out differences. That said, forecast errors and dispersion are of course influenced by analyst
behavior. Consequently, we investigate their overlap with our measure (earnings adjustments).
We find that (i) the correlations are low, (ii) including forecast errors and dispersion as control
variables in our main tests leave results unaffected, and (iii) when using forecast errors and
dispersion, respectively, as the dependent variable within our test design there is no statistical
association with IFRS adoption. We conclude that analyst earnings adjustments do not have the
same empirical properties as forecast errors and forecast dispersion.
We next investigate cross-sectional determinants of the IFRS adoption effect, beginning
with legal enforcement and the differences between domestic standards and IFRS (“accounting
distance”). Prior research has indicated that IFRS effects (of various kinds) are influenced by
these two dimensions (e.g., Daske et al. 2008, Pope and McLeay 2011). We use ordered
categorical input data referenced in prior work and develop a confirmatory factor analysis
approach to derive latent variables for both enforcement and accounting distance. We believe
9
Bradshaw (2011) notes that research about the composition of items that analysts exclude would further develop
the research area of earnings adjustments.
5
these latent variables are more powerful proxies for variation in enforcement and accounting
distance than those used in previous research. We find that the analyst adjustment effect of IFRS
adoption is significantly more pronounced in countries with stricter enforcement, and/or larger
accounting distance, although the main IFRS effect is not contingent on enforcement or distance.
We further verify that firms with poorer earnings quality prior to IFRS adoption experience a
significantly larger IFRS effect, i.e., a larger decrease in earnings adjustments. We believe these
cross-sectional results support the construct validity of analyst adjustments as a measure of
earnings quality.
Next, we attempt to distinguish between comparability and more general earnings quality
effects. While comparability is an important dimension of decision usefulness according to
IASB’s conceptual framework, we want to investigate whether more mechanical accounting
standard comparability (when all firms report under a common set of standards) is a significant
driver of lower analyst adjustments following IFRS adoption. We examine this question in two
ways. We first note the absence of a 2005 effect for voluntary adopters who had previously
shifted to IFRS, which indicates no significant comparability effect when all other firms move to
IFRS in 2005. Second, within the mandatory adopter sample, we investigate whether the IFRS
adoption effect is more pronounced for firms that prior to IFRS adoption were covered by
analysts who followed firms reporting under different local accounting standards (as would be
expected if accounting standard comparability is a significant driver of the effect). The results
do not support this conjecture. Overall, we conclude that accounting standard comparability is
not, in and of itself, an explanation for the decreased analyst adjustments following IFRS
adoption.
6
We perform several additional tests in order to evaluate the robustness of our findings.
First, to investigate whether the decrease in analyst adjustments can be attributed to a learning
effect around IFRS adoption, we examine the prior IFRS experience in the group of analysts
following a firm and, separately, the frequency of non-zero adjustments in the first year
following adoption. We find no support for a material effect of prior experience or learning on
our results. Second, we recognize that, as a consequence of IFRS, fair values were introduced
for certain financial instruments, investment property and biological assets. Excluding firms in
the financial, real estate and forestry industries does not materially affect results. Third, the
accounting for goodwill changed from annual amortization to annual impairment tests in several
countries. Excluding firm-years with a decrease in goodwill does not affect results. Fourth, we
test whether our results are sensitive to scaling our main variable with total assets, which might
be affected by the change in accounting principles. We do not find that the scaling affects
results.
In summary, we interpret the results for mandatory and voluntary adopters as follows.
First, financial analysts perceive firms’ reported earnings to be of higher quality subsequent to
IFRS adoption.
Second, the decrease in analysts’ adjustments following IFRS adoption is
substantial regardless of type (mandatory or voluntary) and timing (2005 or earlier years). Third,
the effect does not appear to be driven by a mechanical increase in comparability when firms all
use IFRS; nor does the analyst adjustment effect appear to be driven by confounding events
around 2005.
The paper proceeds as follows. In Section 2, we discuss the related literature and develop
the hypotheses. Section 3 describes the research design and provides sample statistics. Section 4
7
presents the main results, and Section 5 contains various additional tests and sensitivity analyses.
Section 6 concludes.
2.
Background and research questions
In order to make an empirical-archival assessment of how analysts perceive the quality of
reported earnings produced under different sets of accounting standards, one needs an
operational measure of analyst behavior that (i) includes reported earnings, and (ii) has properties
consistent with notions of “earnings quality”. We investigate analysts’ adjustments to reported
earnings before and after a large-scale change to accounting standards: the introduction of IFRS
in the European Union and the European Economic Area. Strictly speaking, we believe that
studying how analyst adjustments, as a measure of analysts’ processing of earnings information,
are affected by changes to accounting standards is a topic interesting to study in its own right,
without necessarily associating adjustments with notions of “quality”.
However, given the
intense (and still unsettled) debate about how IFRS adoption has affected earnings quality and
associated capital market outcomes, we believe the results can inform the IFRS debate as well.
Dechow et al. (2010) note the existence of multiple earnings quality definitions and
conclude that statements about the quality of earnings must be contingent on the decision context
and the information relevant to a particular user or decision maker. We focus on decisions made
by financial analysts in their processing of earnings information and view the magnitude of their
adjustments as an inverse indicator of the quality of earnings, as perceived by analysts. This
definition of earnings quality will include adjustments intended to increase earnings persistence
(by excluding transitory income and expense items), increase value relevance (by excluding
items believed to be irrelevant to investors), and increase earnings comparability across firms (by
adjusting for items that are not similarly accounted for).
8
2.1 Analysts’ adjustments to earnings
Analysts following a specific firm make their own earnings adjustments (potentially in part
guided by management).
When aggregating the forecasts across analysts, IBES uses the
adjustments from the majority of analysts (Christensen et al. 2011). After the firm reports its
earnings, IBES provides its version of adjusted earnings, after applying the adjustments to the
consensus earnings forecast to the firms’ reported earnings (Bradshaw 2011, Christensen et al.
2011). As a consequence, IBES earnings forecasts and IBES-adjusted realized earnings follow
the same basis of calculation. We define earnings adjustments as the difference between the
IBES-adjusted earnings and reported (bottom-line) earnings.
While not explicit in previous research, we believe there are indications suggesting that
analyst adjustments are associated with dimensions of earnings quality. An example, based on
interviews with analysts following FTSE 100 firms (Barker and Imam 2008), concludes that “a
majority of the analysts describe high-quality earnings in terms of some aspect of the ‘core’
earnings of the firm” (p. 319). As a consequence, items perceived as low-quality items are
excluded from the definition of core. For example, excluded items can be transitory or the result
of re-measurement of assets or liabilities, and thus of little perceived value for the prediction of
future earnings. 10 These results are also generally in line with survey data from financial
analysts in the US (e.g., Graham et al. 2002).
10
Common adjustments include impairment losses on fixed assets, impairment or amortization of goodwill, gains
and losses on financial assets as well as fixed assets, restructuring costs. In many of the categories, however,
analysts indicate that the adjustment decision depends which firm they analyze, and there is also variation across
analysts in some of the categories, suggesting that there is no generic template for adjustments. The latter aspect is
further supported by interview evidence in Hjelström et al. (2014). It is also not the case that firms universally
exclude certain items in their calculation of pro-forma earnings (Bhattacharya et al. 2003, Entwistle et al. 2006).
9
Several quantitative studies also focus on the characteristics and capital market
consequences of analysts’ adjustments to earnings.11 For example, Bradshaw and Sloan (2002)
document an increasing trend in both the magnitude and frequency of analysts’ adjustments.
They further find that investors react more strongly to analyst-adjusted earnings than to firms’
reported earnings, suggesting that investors perceive the former as more value relevant. Gu and
Chen (2004) conclude that non-recurring items that analysts do not exclude are less transitory
and more value-relevant than non-recurring items they do exclude, consistent with analysts
having the experience and expertise to make such judgments. There is also evidence that when
analyst adjustments deviate from adjustments made by management, analyst-adjusted earnings
are perceived by investors as more value relevant (Marques 2006, Choi et al. 2007).12
While prior research supports the use of the magnitude of analysts’ earnings adjustments as
an inverse indicator of their perception of earnings quality, research has also suggested that
analysts’ adjustments can be biased. For example, Doyle et al. (2003) find that items analysts
exclude from reported earnings have predictive value for future firm performance. Focusing on
analysts’ incentives, Baik et al. (2009) find that analysts tend to bias adjusted earnings upwards
for so-called glamour stocks but not for value stocks. Analysts can also be (mis-)guided by
managements’ (potentially opportunistic) guidance of pro-forma earnings (e.g., Andersson and
Hellman 2007, Christensen et al. 2011). If analyst bias exists and changes (for any reason)
around 2005, it would constitute a confounding event that may also contribute to a change in
earnings adjustments (we address confounding events in Sections 4.2 and 4.3).
11
As discussed in Bradshaw (2011), several studies with a focus on the manager use analyst-adjusted earnings as a
proxy for management’s pro-forma or non-GAAP earnings. There is a substantial overlap in the adjustments, but
they are not the same. For example, Bhattacharya et al. (2003) use a hand-collected dataset and show that the two
numerically coincide in about 60-70% of cases. Christensen et al. (2011) investigate the links between management
guidance (pro-forma earnings) and analyst adjustments (street earnings).
12
There is to our knowledge no prior research on the variation in analyst adjustments across countries. In related
research, Isidro and Marques (2014) use hand-collected data for 321 large European firms over the years 2003-2005
and investigate management’s propensity to disclose non-GAAP earnings.
10
In summary, our reading of prior literature indicates that (i) the market reacts more to
analyst-adjusted earnings than to reported earnings, (ii) the market puts a higher weight on
analysts’ adjustments than management’s adjustments, (iii) analysts’ inclusions (i.e., items not
excluded from adjusted earnings) are more persistent than exclusions, and (iv) analysts
themselves consider their adjusted earnings to be high quality earnings. We believe these
observations from prior literature lend support to our use of analyst earnings adjustments as a
measure of (perceived) earnings quality. In Section 5.2, we investigate the earnings quality
properties of analyst adjustments within our sample and setting.
2.2 IFRS adoption effects
As mentioned above we believe our results are also informative about the general debate
about IFRS and earnings quality. There is a large literature on this topic, but results are not
consistent. For example, Brüggemann et al.’s (2013, Table 1) review of nine studies that
investigate various earnings quality measures (value relevance, abnormal accruals, earnings
persistence, the association between current period earnings and future cash flows) lists three
studies that find no IFRS effect, three studies that find an improvement after IFRS adoption, two
studies that find a deterioration, and one study finding that the IFRS effect depends on which
accounting property is investigated.
Because the IFRS adoption literature is voluminous, we summarize it in Appendix. Very
briefly, the evidence on the effects of IFRS adoption on various outcome variables (earnings
quality, capital market and other outcome variables) is mixed. The literature also shows that
voluntary adoption effects can differ from those of a mandatory adoption. A general finding is
that IFRS effects tend to exist and or be stronger in countries with stronger legal enforcement
and greater distance between local GAAP and IFRS.
11
Given the varying results in prior literature investigating other earnings quality measures,
we view it as an open empirical question (that to our knowledge has not been previously
investigated) how analysts react to the IFRS adoption in terms of their adjustments to reported
earnings. Our tests measure the overall IFRS effect on analysts’ earnings adjustments, whether
the effect differs for mandatory versus voluntary adopters, whether there is evidence of
confounding events in 2005 (affecting the mandatory adopter tests), various cross-sectional
determinants of the effect (such as a country’s legal enforcement and accounting distance), and
whether the effect is attributable to earnings quality more generally or more narrow
comparability when firms move to a common set of standards.
3.
Research design and data
Our sample of mandatory adopters contains 16,748 firm-year observations of analyst
earnings adjustments from 1999 to 2012.13 This sample covers 1,744 analyst-followed firms
from 19 countries that in 2005 were members of the EU or the European Economic Area. 14 We
require sample firms to report under domestic GAAP until 2004, and under IFRS from 2005
onwards. The firm and firm-year distributions by country are presented in Table 1. As expected,
countries with large equity markets have the largest number of observations (Great Britain,
France and Italy). Some countries have very few observations (the Czech Republic, Hungary
and Slovenia; results are not sensitive to excluding such countries).15 We require firms to have
observations in both the pre- and post-IFRS period, and we require firms to be from countries
with sufficient data to estimate measures of legal enforcement and accounting distance (i.e., a
13
In robustness tests, we exclude 2005. Results are not sensitive to this exclusion.
A few relatively small countries are not included in our sample due to the small number of analyst-followed firms
with sufficient time-series of accounting data (Estonia, Iceland, Latvia, Lichtenstein, Lithuania, Luxemburg, Malta
and Slovakia).
15
In some countries, most notably Austria and Germany, the number of observations for mandatory adopters is
non-trivially lower than the number of analyst-followed firms, because of several firms voluntarily adopting IFRS
prior to 2005. We investigate voluntary adopters in Section 4.2.
14
12
measure of the difference between local GAAP and IFRS, described below).
Firms that
voluntarily adopted IFRS prior to 2005 are analyzed separately in Section 4.2.
Our main outcome variable is analysts’ earnings adjustments, calculated as the absolute
difference between reported (local GAAP/IFRS) EPS and the analyst-adjusted EPS from IBES.16
We use the absolute value of the difference, as we are interested in the magnitude of analysts’
adjustments, not their sign. Following Doyle et al. (2003), Heflin and Hsu (2008) and Kolev et
al. (2008), we scale the adjustments by total assets:17
𝑅𝑒𝑝𝑜𝑟𝑡𝑒𝑑 𝐸𝑃𝑆𝑖,𝑡 − 𝐴𝑛𝑎𝑙𝑦𝑠𝑡𝐴𝑑𝑗𝑢𝑠𝑡𝑒𝑑 𝐸𝑃𝑆𝑖,𝑡
𝐴𝑛𝑎𝑙𝑦𝑠𝑡𝐴𝑑𝑗𝑢𝑠𝑡𝑚𝑒𝑛𝑡𝑠𝑖𝑡 = |
𝑇𝑜𝑡𝑎𝑙 𝐴𝑠𝑠𝑒𝑡𝑠 𝑃𝑒𝑟 𝑆ℎ𝑎𝑟𝑒𝑖,𝑡
|
(1)
We collect reported EPS data from Compustat Global (when the EPS data item is missing
we use net income divided by the number of shares outstanding; results are not sensitive to
excluding these observations). The analyst-adjusted EPS number is ‘EPS Actual’ (described in
Section 2.1) collected from IBES International Summary File (e.g., Bradshaw and Sloan 2002,
Brown and Sivakumar 2003, Doyle et al. 2003). When subtracting analyst-adjusted EPS from
reported EPS, we verify that they are both measured on a primary basis.18
Our main tests investigate whether the magnitude of analyst adjustments changed after the
adoption of IFRS. We document results with and without controls for determinants of analyst
adjustments, such as macro-economic indicators and over-time trends, as well as with countryfixed effects and firm-fixed effects.
16
As explained in Section 2, we use the aggregated adjusted earnings number provided by IBES, following much of
the research based on US data. This design choice, necessitated by data restrictions, precludes the identification of
earnings adjustments made by individual analysts.
17
Some earlier US studies scale the adjustments by stock price; however, this can confound the results both over
time and across countries if there are large systematic increases or declines in prices in some countries. For example,
in some of the sample countries stock prices declined by more than 50% in the 2008-2009 crisis, whereas other
sample countries had substantially smaller losses. The potential drawback of scaling by total assets is that the scaler
itself can be affected by accounting measurement. We address this issue in Section 5.7.
18
In addition, we find individual cases, mostly early in the sample period, where the IBES-based analyst-adjusted
EPS is in Euros and the Compustat-based reported EPS is reported in local currency in countries that had decided to
switch to the Euro. In those cases, we transform the analyst-adjusted EPS to local currencies (note that currency
exchange rates were fixed from 1999, our first sample year, for the countries that adopted the Euro).
13
Panel A of Table 2 contains distributional statistics for our main variable of interest,
AnalystAdjustments, for the sample of mandatory adopters. The mean (median) scaled absolute
adjustments are about 1.74% (0.15%) of total assets per share. The mean (median) is 1.88%
(0.22%) in the pre-IFRS period and 1.63% (0.11%) in the post-IFRS period. The relatively large
difference between the means and medians indicate a presence of some large adjustments. We
note, however, that the relative decrease in the median is larger than the decrease in the mean.
Both parametric and non-parametric tests show that the decrease in the post-IFRS period is
statistically significant (using a t-test and a Wilcoxon test, two-sided p-values are 0.0004 and
0.0204, respectively).
Panel B of Table 2 reports descriptive statistics for the voluntary adopter sample, which
comprises 1,115 firm-year observations for 116 firms that voluntarily adopted IFRS between
1999 and 2004. We exclude firms that reported according to other non-domestic accounting
principles (e.g., US GAAP). The final sample of voluntary adopters contains firms from 11
countries, with a concentration from Germany (62 firms). The mean (median) absolute analyst
adjustment is 1.87% (0.23%) of total assets in the years prior to IFRS adoption and 0.93%
(0.03%) in the years after IFRS adoption (the mean decrease is significant at the .0002 level; the
median decrease is significant at the .0001 level).
Panel C of Table 2 reports descriptive statistics for variables that we use to investigate
cross-sectional variation in the IFRS effect on analyst adjustments (results are reported in
Section 5.2). The first one is the pre-IFRS level of absolute discretionary accruals, AbsDiscrAcc,
based on the modified Jones (1991) model. We estimate the model using the cross-sectional
approach from Ecker et al. (2013), where peer firms are identified by size (lagged total assets).
14
As mentioned in Section 2.2 and Appendix, several studies indicate that a country’s legal
enforcement and the accounting distance between local GAAP and IFRS matter significantly
when assessing IFRS effects for various earnings quality and capital market outcome variables.
To ensure that we measure these constructs as efficiently and as close to 2005 as possible we
create variables as follows. Enforcement measures the strength of the country-level regulatory
enforcement in 2005, based on an enforcement factor from a confirmatory factor analysis on
three categorical input variables.19 We start by collecting all enforcement indicators for the year
2005 from Brown et al. (2014) as our initial set of input variables. Brown et al. survey data from
the International Federation of Accountants (IFAC), complemented by data from the World
Bank and Commission of European Securities Regulators (CESR). The items include data on
the existence, work, activity and resources of the enforcement bodies.20
In a preliminary step to create our enforcement factor, we exclude variables that are
constant, and if two variables are perfectly correlated we exclude one of them as they contain no
incremental information about the latent variable for enforcement rigor.
Enforcement is
ultimately based on three categorical input variables: specifically, whether a regulatory body (i)
reviews financial statements, (ii) takes or has taken enforcement actions, and (iii) the number of
staff of the regulatory body. Our confirmatory factor analysis treats variables (i) and (ii) as
binary, while variable (iii) can take on three (ordered) values. The Enforcement factor is the
weighted combination of the three input variables that maximizes the log likelihood from three
19
Muthen (1984) develops the mapping from categorical input variables to continuous latent variables. The specific
estimator we use (weighted least squares, with a mean-variance adjustment, WLSMV) is validated relative to
maximum-likelihood estimators in Beauducel and Yorck Herzberg (2006). See also Wang and Wang (2012) for a
comprehensive explanation of this approach, while Timm (2002) provides a more general description of structural
equation modeling (SEM).
20
The detailed variable descriptions are in Brown et al. (2014). Their Table 2 contains the variable definitions and
the data sources; while Appendix 2 lists the data on the input variables itself, by country.
15
probit regressions on the factor. Larger values for the enforcement factor correspond to higher
enforcement rigor.
Our accounting distance factor is also constructed with confirmatory factor analysis across
all sample observations. Our input variables are defined in the following way. For each country,
we begin by coding a severity score for accounting differences between local (pre-IFRS) GAAP
and IFRS, corresponding to the severity categorization in Nobes’ (2001) GAAP survey. To
reduce complexity and ensure convergence of the factor estimation, we focus on the standards
level (not the paragraph level), by assigning the highest severity score across all paragraphs to
the standard. In addition, we reduce the input to the five standards with the highest severity
score in our sample (i.e., those that differ most often and most severely from IFRS). Those five
standards are, in decreasing order: IAS19 (pensions), IAS22 (consolidation), IAS39 (financial
instruments: recognition and measurement), IAS32 (financial instruments: presentation) and
IAS35 (discontinued operations). The AccountingDistance factor is the weighted combination of
the five input variables that maximizes the log likelihood from five probit regressions on the
factor. Larger values for AccountingDistance correspond to larger distance between local GAAP
and IFRS.
Panel C of Table 2 indicates substantial cross-sectional variation when compared to
the measures of central tendency in the three variables defined above (AbsDiscrAcc,
Enforcement, AccountingDistance).
4.
Main results
This section describes our main results for mandatory IFRS adopters (Section 4.1) and
voluntary adopters (Section 4.2), tests against a benchmark US sample (Section 4.3), and tests
using a statistically inferred number of analyst adjustments (Section 4.4).
16
4.1 Mandatory adopters
The main test design includes an event indicator for IFRS adoption (PostIFRS) and macroeconomic determinants of analyst adjustments.
To control for country- and firm-specific
determinants, we report results including country- and firm-fixed effects. The basic design
structure follows Equation (2), below, and is similar to that in Cohen et al. (2008) who study
earnings management before and after the introduction of the Sarbanes-Oxley regulation in the
United States:
𝐴𝑛𝑎𝑙𝑦𝑠𝑡𝐴𝑑𝑗𝑢𝑠𝑡𝑚𝑒𝑛𝑡𝑠𝑖𝑡 = 𝛼0 + 𝛼1 𝑃𝑜𝑠𝑡𝐼𝐹𝑅𝑆𝑡 + 𝛼2 𝐶𝑟𝑖𝑠𝑖𝑠𝑗𝑡 + 𝛼3 𝑇𝑖𝑚𝑒𝑡 + 𝜀𝑖𝑡
(2)
AnalystAdjustments is the absolute value of the analyst adjustments by firm and year, as
defined in Equation (1). PostIFRS is an indicator variable that takes the value of 0 (1) for preIFRS (post-IFRS) observations. Crisis is a variable specific to country j that takes the value of 1
if GDP growth (reported by the World Bank) is negative and zero otherwise. We include Crisis
as a control variable to capture the fact that certain common adjustments such as impairment
charges and restructuring charges are more likely in crisis years, and the distribution of crisis
years may not be equal before and after the IFRS adoption year or across countries. Time is equal
to the difference between the year of the observation and 1999 (the first year in our sample
period), included to capture a potential time trend in earnings adjustments documented by, for
example, Bradshaw and Sloan (2002) and Brown and Sivakumar (2003).
Table 3 reports results using either country-fixed effects (columns 1–3) or firm-fixed
effects (columns 4–6). Results are similar, and for brevity we concentrate on the firm-fixed
effects results, which control for firm-specific determinants of analyst adjustments that are
relatively stable and not captured by other variables.
Such determinants include variables
proxying for the complexity of the business model, such as intangibles intensity (Heflin and Hsu
17
2008), the management’s propensity to disclose own adjustments to earnings in the calculation of
its own non-GAAP earnings numbers (Christensen et al. 2011), as well as (portions of)
adjustments driven by analysts’ incentives to promote certain stocks (Baik et al. 2009).21
We first estimate a reduced form of Equation (2) that includes only the indicator variable
PostIFRS. Similar to the descriptive statistics in Table 2, the test shows a significant decrease in
the magnitude of analyst adjustments following IFRS adoption, with a point estimate of −0.20%
of total assets (t = −2.97; firm-fixed effects included). When we add Crisis to control for
adjustments specific to poor macro-economic conditions, the point estimate on PostIFRS
increases in magnitude to −0.30% (t = −4.27). Finally, the general time trend found in US data is
also present in international data, with a point estimate of 0.08% of total assets per year
(t = 5.08). The time trend is not significantly different in the pre- versus post-IFRS periods (the
p-value for the difference in Time is 0.55, not tabulated).
Taking the time trend into
consideration leads to a greater general decrease in the magnitude of adjustments after the IFRS
transition, 0.81% of total assets per share (t = −6.62).
Overall, Table 3 shows that after mandatory IFRS adoption, the magnitude of analysts’
earnings adjustments decrease significantly regardless of the choice of control variables and
regardless of whether we use country-fixed effects or firm-fixed effects (t-statistics range from
−2.97 to −6.62). The decrease is also economically meaningful. For example, the decrease from
the average pre-IFRS adjustment level with (without) control variables and firm-fixed effects is
43.1% (10.6%).22
21
Another potential advantage of using firm-fixed effects rather than explicit control variables is that proxies for the
latter are subject to changes in the accounting measurement rules as a consequence of IFRS adoption, even as the
fundamental construct of interest remains constant.
22
The 43.1% decrease is the coefficient estimate of the IFRS decrease from Table 3 (0.81%) compared to the
average pre-IFRS level in Table 2 (1.88%). The 10.6% decrease is the coefficient estimate of the IFRS decrease
from Table 3 without control variables (0.20%) compared to the average pre-IFRS level in Table 2 (1.88%).
18
A potential concern with any pre- versus post- event study is the attribution of an effect to a
particular regulatory event when other factors may change concurrently (see for example the
discussion in Christensen et al. 2013). We address the question of confounding events in two
ways. First, we investigate the analyst adjustment effect in a sample of voluntary adopters, all of
whom switched to IFRS prior to 2005. Because the event year is not clustered in any particular
calendar year in our sample, IFRS adoption effects found for voluntary adopters are not likely to
be due to potential confounding events in or around 2005. Second, we re-estimate our main tests
using a difference-in-difference design with a US control sample (which is unaffected by IFRS
adoption).
4.2 Voluntary adopters
Table 4 reports the results from regression (2) for the voluntary adopter sample, using firmfixed effects (country-fixed effects results are similar and not tabulated). Results in Columns 1,
2 and 3 are qualitatively similar to the mandatory adopter results in Table 3 in that the PostIFRS
effect is significantly negative across specifications, with point estimates ranging from −0.90%
to −1.01% (t-statistics range from −2.87 to −3.60). The magnitude of this effect corresponds to a
48-54% decrease from the average pre-IFRS-adoption level. Compared to the mandatory adopter
sample, the IFRS effect for voluntary adopters is somewhat larger (comparing Table 4 to Table
3); however, the difference is not significant.23 Unlike the results for mandatory adopters, the
time trend variable (Time) and control for crisis years (Crisis) are not significant at conventional
levels. Overall, we conclude that the decrease in analysts adjustments around IFRS adoption is
23
We perform a difference-in-difference analysis including both the mandatory adopter sample and the voluntary
adopter sample, where a treatment indicator variable, MandatoryAdopt (1 for mandatory adopters and 0 for
voluntary adopters) is interacted with the PostIFRS variable. The test design remains unchanged in all other
respects. Results (not tabulated) show that the coefficient on PostIFRS is negative and significant (−0.0106; t =
−2.51), whereas the coefficient on the interaction term PostIFRS ×MandatoryAdopt is not (0.0021; t = 0.47). In
short, there is no significant difference between the early and firm-specific IFRS effect for voluntary adopters and
the 2005 IFRS effect for mandatory adopters.
19
economically and statistically meaningful, regardless of the timing (2005 or earlier) and
regardless of the type of adoption (mandatory or voluntary).
In Columns 4 and 5, we introduce Post2005, which takes the value 0 for the years 1999 to
2004 and 1 thereafter. We introduce this “pseudo-event” variable for two reasons. First, we
want to ensure that our PostIFRS variable for voluntary adopters is not a noisy proxy for 2005
(recall that one of the reasons for the voluntary adopter analysis is to rule out potential
confounding events in 2005, the mandatory adoption year). Second, the variable allows us to test
for any incremental effect for voluntary adopters in 2005.
In Column 4, we note that Post2005 is not significant (t = 0.74), nor does its inclusion
meaningfully alter coefficients on other variables. Specifically, the firm-specific PostIFRS effect
remains significant (t = −2.93). In Column 5, we include only Post2005 and drop the firmspecific PostIFRS variable. Again, the coefficient on Post2005 is insignificant (t=0.48). We
conclude that the firm-specific PostIFRS variable does not proxy for a general 2005 effect (a
possibility that cannot be ruled out in the analysis of mandatory IFRS adopters). We believe this
result supports our interpretation that the improvements in earnings quality, as proxied by the
decrease in earnings adjustments, are attributable to the shift in accounting standards.24
4.3
Difference-in-difference analysis with a US control sample
As indicated in the prior section, we believe that the lack of a significant 2005 effect for
pre-2005 voluntary adopters speaks against confounding events in 2005 driving results for the
mandatory adopters. To further probe such concerns with the mandatory adopter sample, we use
a difference-in-difference design with a matched control sample of analyst-followed US firms,
24
In addition, the insignificant Post2005 effect for the voluntary adopters indicates no discernible additional
comparability effect for the early voluntary adopters at the time of the general IFRS adoption in 2005. We discuss
the comparability issues in detail in Section 5.3.
20
the construction of which follows the construction of our main sample.25 We match these firms
to our main sample along two dimensions: (i) the most recent pre-event industry classification
based on the two-digit SIC code, and (ii) the minimum absolute distance (MAD) between preevent levels of absolute earnings adjustments.26 Our aim is to control for the firm’s business
model and operating environment, as proxied by industry, as well as for the pre-2005 level of
analysts’ earnings adjustments. In other words, we have similar firms with similar unaffected
starting levels of analyst adjustments, allowing us to isolate the effects of a change in standards
(the IFRS sample only) from otherwise similar but unaffected firms (the US sample).
The final sample in this analysis has 31,852 firm-year observations, with an average
(median) MAD of 0.0018 (0.0001). 27 The firm-fixed effects regression includes the main
variables Post2005, Crisis and Time, as previously defined, and interacts each variable with an
indicator for the firm being an IFRSAdopter (treatment firm). Results, reported in Table 5, show
that the coefficient on a 2005 effect for US control firms is small and insignificant (−0.0006;
t = −0.40), whereas the coefficient on Post2005 interacted with IFRSAdopter is negative and
significant (−0.0073; t = −3.58). We interpret these results as supporting our main results for
mandatory adopters: the decrease in analysts’ earnings adjustments is an IFRS effect and not a
general decrease around 2005 in the magnitude of these adjustments.
25
We impose the same restrictions on the US sample as on our IFRS sample and require that firms have at least one
observation before and after 2005, respectively. In addition, because prior work (Marques 2006, Heflin and Hsu
2008, Kolev et al. 2008) has documented a discrete downward shift in analyst adjustments following the SEC
disclosure requirement on pro-forma reconciliations in 2002 (Regulation G), we perform this test for a sample
period beginning in fiscal year 2003. While this regulation applied to companies domiciled in the US it is
conceivable that the regulation had spill-over in our sample countries. Since the sample in this test is restricted to
observations from 2003 and onwards, this test also controls for potential effects in our sample countries due to the
US regulation. Our initial US sample comprises 3,909 firms from which we draw the matched firms.
26
The pre-event level of absolute earnings adjustments is computed as the average over all pre-event years with the
necessary data. In the rare cases where the MAD does not yield a single matching firm, a firm is selected randomly
from the firms with equal MAD.
27
The sample loss for IFRS firms is from 92 firms not having pre-event SIC data, and 6 firms with SIC 89 not
having matches in the US sample.
21
4.4
Approximating the number of exclusions
So far, our analysis has been focused on the effect of IFRS on the magnitude of analysts’
earnings adjustments. Conceptually, the same arguments that we use to motivate the magnitude
of adjustments as the variable of interest should also hold for the number of adjustments. In this
section, we statistically infer how many and which line items the (majority of) analysts
exclude. We aim to explain the (signed) adjustments to reported earnings by a combination of
income statement line items on Compustat Global. Because these adjustments may be firmspecific and time-varying, our approach is independently applied to each firm-year.
The approach takes the following steps. First, to reduce computer processing time, we preselect 20 income statement line items from Compustat Global that we believe, ex ante, are likely
candidates for analysts’ exclusions.28 We estimate the EPS effect of those line items by first
transforming before-tax line items into after-tax values, and by scaling all line items by the
number of shares on Compustat. 29 The sign of all items is standardized such that positive
(negative) values reflect an expense (income). In the following discussion, we refer to these
standardized EPS effects as “line items” for brevity. For each observation, we identify the subset
of ki,t line items, out of the 20 in total, whose values are non-missing and non-zero.
The sample is reduced to 15,089 firm-years by requiring data for the number of shares on
Compustat (−57 firm-years), requiring at least one line item with a value (ki,t ≥1) (−11 firm28
We supplement income statement items with less aggregated items that are classified as cash flow line items in
Compustat. The 20 pre-selected line items are: amortization of intangibles (Compustat item AM), income or loss
from discontinued operations (DO), equity in earnings of associated companies (EIEAC), foreign exchange income
(FCA), interest and related (dividend) income (IDIT), interest and dividend adjustments (INTOACT), minority
interest / non-controlling interest (from income statement, MII), other net items (NIO), total net items (NIT), nonoperating income (NOPI), provisions (PRV), special items (SPI), gains from the sale of property, plant and
equipment and investments (SPPIV), deferred taxes on the income statement (TXDI) and as reported on the
statement of cash flows (TXDC), other operating expenses (XOPRO), pension and retirement expense (XPR),
research and development expense (XRD), and rental expense (XRENT).
29
We approximate the tax rate as total tax expense over pre-tax income (items TXT and PI, respectively). If the
result fall outside an admissible range of 0% to 60%, we assumed a 30% tax rate. For lack of data on the number of
shares on IBES, we use Compustat Global item CSHPRIA, or, if missing, item CSHOI.
22
years). We eliminate firm-years with no adjustments (−1,591 firm-years), because an adjustment
of zero is uninformative. It cannot distinguish among the following three cases: the analyst
adjusts nothing; adjusts an indeterminate number of line items whose values are zero, or adjusts a
combination of line items that sum up to zero.
 k i ,t 


r
ri , t  1  i , t 
k i ,t
The algorithm tests all possible distinct combinations of line items, 
of every combination for each
ri , t  1, 2 , ..., k i , t 
.
, i.e., the sum
The evaluation criterion is the absolute
difference between the exclusion and the sum of the ri,t line item values. For ri,t = 1, each of the
ki,t non-zero line items is evaluated separately; for ri,t = 2, all distinct combinations of two line
items are evaluated, etc. Combinations with higher order (ri,t) need to explain strictly more of
the adjustment amount than lower-order combinations.
Thus, the iteration identifies the
combination of ri,t line items whose sum is closest to the adjustment amount; if multiple
equivalent solutions exist, solutions with a smaller ri,t (i.e., fewer line items) are given
preference.30
We acknowledge that ri,t is prone to unavoidable measurement error from three main
sources. First, our pre-selected 20 candidate line items may not include all line items analysts
adjust for. Second, the number of shares used by analysts may differ from the Compustat
number of shares. Third, and most importantly, we rely on the Compustat classification and
aggregation of line items. The iteration matches line item combinations with the adjustment
amount, so it will not identify the correct number of line items if analysts exclude an expense
category that is either not recorded or recorded with a different value on Compustat, or if
analysts only partially adjust a Compustat line item. In addition, the likelihood of identifying a
30
While the algorithm determines the optimal number of line items ri,t, the main variable of interest, there were rare
cases of multiple equivalent solutions within a given level of ri,t. In those cases, we drew the specific combination
of line items randomly.
23
solution for ri,t decreases when the (absolute) magnitude of the adjustment decreases. In the
limit, as discussed above, adjustments of zero magnitude need to be dropped from the sample,
but on a conceptual level they are informative about a reduction in adjustments after IFRS.
Finally, the algorithm is not guaranteed to converge to a solution. It will, for example, fail when
each of the non-zero candidate line items has the same sign and is of higher (absolute) magnitude
than the total adjustment itself. For these reasons, the final sample is further reduced by the
2,506 firm-years for which no solution was obtained.
In our final sample of 12,583 observations, the number of non-zero candidate line items,
ki,t, ranges from 1 to 15, with a mean (median) of 8.09 (8). The average (median) ri,t is about
3.36 (3), and ranges from 1 to 11 line items. The three most frequently excluded items,
conditional on a non-zero value on Compustat, are SPI (38.77% of cases), SPPIV (38.44%) and
FCA (36.92%). As a comparison, Gu and Chen (2004) investigate analysts’ adjustments of nonrecurring items in US firms between 1993 and 2002. While both the sample and time period are
different from ours, we note that items corresponding to SPI and SPPIV rank among the highest
adjustment categories also for them, which we (cautiously) interpret as supporting the validity of
our method.31
We repeat the firm-fixed-effects regression (2), replacing the absolute magnitude of the
adjustments with the number of adjusted line items, ri,t, as the dependent variable. Controlling
for firm-fixed effects, a general time trend and crisis years, the coefficient on PostIFRS is
−0.1347 with a t-statistic of −2.49. We further subset our sample by the percentage of the
absolute adjustment that is unexplained by the identified line items.
After excluding
observations above the sample median of about 6.98%, the coefficient on PostIFRS is −0.2105
(t = −2.41), despite reducing the sample by half. Second, the inclusion of voluntary adopters in
31
ri,t equals ki,t for only 132 firm-years, alleviating concerns about starting with 20 pre-selected line items.
24
the sample hardly affects quantitative results. Finally, we remove the restriction that a firm must
have observations both before and after IFRS adoption. This increases the sample size to 21,695
firm-years (4,922 distinct firms); the coefficient on PostIFRS increases to −0.2167 (t = −4.59).
Overall, and despite the empirical caveats (potentially severe measurement error) discussed
above, the evidence in this section supports the conclusions from our main results on the absolute
magnitude of the analyst adjustments.
5.
Additional analyses
In this section we present various validity and robustness tests. Specifically, we test for a
potential association between analyst adjustments and analysts’ forecast errors and forecast
dispersion (Section 5.1), we investigate the cross-sectional properties of the decrease in earnings
adjustments (Section 5.2), we address the issue of whether the decrease in adjustments is (at least
partially) explained by higher comparability in the post-IFRS period (Section 5.3), and we
perform a number of robustness tests (Sections 5.3 to 5.7).
5.1 Analyst adjustments versus forecast errors and dispersion
The Appendix discusses studies investigating analyst forecast errors and dispersion before
and after IFRS adoption. These measures are also influenced by analyst behavior, but they are
distinct from analysts’ adjustments to earnings (our main measure) since they do not include
information on reported (GAAP or IFRS) earnings. Specifically, forecast errors and forecast
dispersion are typically measured at the adjusted (non-GAAP/non-IFRS) earnings level.
To investigate the empirical overlap between our measure and forecast errors and
dispersion, we first construct average absolute forecast errors from IBES and collect IBES’
reported forecast dispersion.
The Pearson correlation (not tabulated) between the average
absolute forecast error and absolute analyst adjustments is 0.1134 (significant at the .001 level).
25
The Pearson correlation between forecast dispersion and absolute analyst adjustments is 0.0874
(significant at the .001 level).
Next, we re-estimate our main test (Table 3, column 6), but substitute absolute forecast
errors and dispersion for absolute analyst adjustments. To the extent that the IFRS transition has
generally enhanced the information environment also forecast errors and dispersion may show an
improvement. However, if analysts are effective in achieving the preferred adjusted earnings
number regardless of the starting point (local GAAP or IFRS), forecast errors and dispersion
cannot inform about differential properties of reported earnings since the adjustment process can
dampen or even cancel out differences. In contrast to our main results using analyst adjustments,
we do not find an IFRS effect on forecast errors and forecast dispersion.32
In untabulated tests, we further re-estimate our main tests from Table 3 but include absolute
forecast errors and, separately, forecast dispersion as control variables. Both the point estimates
and the t-statistics for PostIFRS are virtually unchanged. We conclude that, while absolute
analyst adjustments are correlated with forecast errors and dispersion, the measures do not
capture the same construct in our setting.
5.2 Absolute earnings adjustments interpreted as earnings quality
In Section 2.1 we referenced survey studies where analysts themselves state that they adjust
earnings in order to increase earnings quality and we noted results in the US-based capital
markets literature that investors react more to adjusted earnings than to bottom-line earnings,
consistent with the former being of higher quality (for valuation purposes). Consequently, we
interpret the magnitude of analysts’ earnings adjustments as an inverse measure of earnings
32
As discussed in Appendix A, empirical results in prior literature on forecast errors and forecast dispersion vary.
We speculate that these measures are relatively sensitive to test designs. Consequently, we do not interpret the null
results using our test design as conclusive evidence on whether IFRS adoption has led to effects on forecast errors
and/or dispersion. We note, however, that these measures do not have the same empirical properties as analyst
adjustments.
26
quality as perceived by analysts. To further validate this interpretation within our sample we
investigate the cross-sectional variation in the IFRS effect in three settings where we believe
there is a relatively clear prior on a more pronounced effect (specifically, for firms with ex-ante
poor earnings quality, in countries with high enforcement and in countries with high accounting
distance).
To test for various cross-sectional determinants of the IFRS effect, we augment Equation
(2) as follows:
𝐴𝑛𝑎𝑙𝑦𝑠𝑡𝐴𝑑𝑗𝑢𝑠𝑡𝑚𝑒𝑛𝑡𝑠𝑖𝑡 = 𝛼0 + 𝛼1 𝑃𝑜𝑠𝑡𝐼𝐹𝑅𝑆𝑡 + 𝛼2 𝑇𝑖𝑚𝑒𝑡 + 𝛼3 𝐶𝑟𝑖𝑠𝑖𝑠𝑖𝑡
+𝛼4 𝑃𝑜𝑠𝑡𝐼𝐹𝑅𝑆𝑡 × 𝐷𝑒𝑡𝑒𝑟𝑚𝑖𝑛𝑎𝑛𝑡𝑖(𝑗) + 𝜀𝑖𝑡
(3)
where Determinanti(j) represents prior earnings quality, enforcement and accounting
distance, respectively.33
In Table 6 we report the results of the cross-sectional tests. The first column contains the
results with AbsDiscrAcc, the absolute discretionary accruals as described in Section 3, which is
a conventional statistical measure of earnings quality. 34 We expect that firms with ex-ante
higher AbsDiscrAcc (poorer earnings quality in the pre-IFRS period) should experience a larger
decrease in earnings adjustments following IFRS adoption. Results are consistent with this
hypothesis as indicated by the significantly negative interaction effect between AbsDiscrAcc and
PostIFRS (t = −5.45).35
The next interaction variable is the latent variable Enforcement, constructed using a
confirmatory factor analysis on categorical input variables as described in Section 3.
33
As
We omit a main effect of the determinants as they do not vary over time and are thus captured by the firm-fixed
effects.
34
Because of data requirements AbsDiscrAcc has a lower number of observations (n=14,286).
35
In non-tabulated tests, we also test the PostIFRS interaction with an alternative proxy for earnings quality, the
absolute value of the residuals from a cross-sectional regression of working capital accruals on prior period, current
period and next period cash flows from operations, augmented by net property plant and equipment and change in
sales, following Dechow and Dichev (2002) and McNichols (2002). Results are economically and statistically
similar to those obtained using AbsDiscrAcc.
27
discussed in Section 2.2, the consequences of IFRS adoption are still under debate in the
literature. However, several studies note the importance of a country’s enforcement regime,
either as a main effect or interacted with an IFRS transition variable (e.g. Daske et al. 2008,
Barth and Israeli 2013, Christensen et al. 2013). Following this literature, we expect the IFRSrelated decrease in absolute earnings adjustments to be more pronounced when the level of
enforcement is higher. The results in Column (2) of Table 5 indicates that this is the case (t
=−2.84).36
The third interaction variable is the latent variable AccountingDistance, the construction of
which is also described in Section 3. Its inclusion is motivated by studies that hypothesize and
find more pronounced IFRS effects in countries whose domestic GAAP is more dissimilar to
IFRS (e.g., Bae et al. 2008, Byard et al. 2011, Christensen et al. 2013, Cascino and Gassen
2015). We find a statistically significant IFRS interaction effect associated with accounting
distance in our sample (t = −2.53). The result suggests that analysts reduce their adjustments
after IFRS adoption even more for firms that previously reported under a more distinct (from
IFRS) domestic GAAP.
Combined, the results in Table 6 indicate that the magnitude of absolute earnings
adjustments have properties expected from a measure of earnings quality. We additionally note
that, regardless of which interaction variable is included, the coefficient on our main variable of
interest, PostIFRS, remains significant (t-statistics range between −4.03 and −6.71).
36
There is also literature highlighting the importance of the change in enforcement (Christensen et al. 2013). Brown
et al. (2014) provide sufficient information to estimate enforcement measures not only for 2005, but also for 2002
and 2008. To calculate the change in enforcement between the pre- and post-adoption periods, we estimate
additional enforcement factors for 2002 and 2008 and calculate the change. When we use this change in
enforcement, results are nearly identical for the coefficient on PostIFRS, and the interaction with the change in
enforcement loads qualitatively similar to the enforcement level interaction in the table.
28
Consequently, our main IFRS effect is influenced by, but not contingent on, for example high
enforcement or high accounting distance.
5.3 Comparability effects
While the IASB’s conceptual framework specifies comparability as an enhancing
qualitative characteristic of decision-useful information, some decrease in analyst adjustments
following IFRS adoption could follow mechanically when firms shift from the use of various sets
of (domestic) standards to the use of one common set of standards. 37
To address the
comparability issue, we make the following observations and tests.
We first note the strong results for voluntary adopters (Table 4). Because voluntary
adopters’ choices of adoption dates are (relatively) independent of other firms’ choices in a given
analyst’s sector coverage, any adjustment-decreasing effect is less likely to be driven by
comparability only. The reason is that voluntary IFRS adopters must be benchmarked against
not-yet-adopting firms continuing to report under various domestic sets of standards.
In
addition, the subsequent mandatory adoption of other firms would constitute a substantial
increase in comparability across all firms. If comparability is a significant driving force behind
the decline in adjustment magnitude, one would expect voluntary adopters to experience an
effect also in 2005. The results in Table 4, Columns 4 and 5, show that there is no separate or
incremental 2005 effect for voluntary adopters, which we interpret as inconsistent with
comparability effects driving the results.
Next, we investigate the comparability issue within the mandatory adopter sample.
Specifically we construct a variable, AnalystForeignCoverage, which proxies for whether a firm
37
Clearly, accounting standard comparability cannot be the full explanation for analysts’ adjustments, as is
evidenced by the prevalence of analyst adjustments in the US, where firms report under the same set of accounting
standards.
29
is followed by analysts with cross-border coverage prior to IFRS adoption.38 Analysts who prior
to 2005 followed firms reporting under different sets of accounting standards potentially made
adjustments to mechanically increase comparability across firms in their coverage portfolios. To
the extent the decrease in analyst adjustments is largely driven by such mechanical comparability
effects rather than more general earnings quality effects, we expect AnalystForeignCoverage to
have a negative interaction effect with PostIFRS.
In untabulated tests, we find that the
interaction effect is actually positive. We interpret this result as evidence that mechanical
comparability is not the main driver of the IFRS effect on analysts’ earnings adjustments.
5.4 Analyst learning
A potential alternative explanation for the result that analysts’ adjustments decrease in
magnitude after a firm’s IFRS adoption is that analysts initially make fewer or no adjustments
because they are not familiar with the new accounting regime (see, for example, Ernstberger et
al. 2008, who document higher forecast errors in the year of the transition). While we believe
this explanation is unlikely, given the finding in Section 5.3, we nevertheless check the
frequency of zero adjustments over the sample years. If analysts make few or no adjustments
because of lack of experience with IFRS, we would expect more zero adjustments in 2005
compared to the pre-IFRS period. We find the opposite, however. Zero-adjustments are slightly
less frequent in 2005 (and the following years) compared to the pre-IFRS period.39
38
AnalystForeignCoverage takes on a value of 1 if at least 50% of the firm’s analysts over the pre-IFRS years also
covered at least one firm in the European Union / European Economic Area that reported under a different
(domestic) standard. A zero value indicates cases where the majority of analysts covered firms following the same
domestic standard. We note that our foreign coverage variable does not speak to the analysts’ domicile relative to
the firms in the covered sector (as does, e.g., the definition in Tan et al. 2011), but rather the domicile of the covered
firms.
39
A tangential point relates to analysts’ prior experience with IFRS, i.e., analysts following other firms that had
voluntarily adopted IFRS prior to 2005. To test this possibility, we measure the proportion of a firm’s analysts in a
given year (in the pre-2005 period) that also follow at least one IFRS firm. We next construct a variable,
ExperienceIFRSi, by averaging the proportions over the pre-2005 years. In other words, ExperienceIFRSi is meant
to capture the “IFRS intensity” among the firm’s analysts. We then add an interaction variable of ExperienceIFRSi
30
To the extent analysts and preparers (firms) are uncertain about implementation issues, the
first few years might also not be representative of longer-term IFRS effects. We check the
sensitivity of our main results to this issue by excluding the first 1, 2 and 5 years following the
IFRS adoption from the analysis, respectively. The sample size decreases, but inferences do not
change (the t-statistics for the main IFRS effect is −4.14, −3.49 and −2.93 when excluding 1, 2
and 5 years of data, respectively). Overall, we conclude that, while learning effects cannot
absolutely be ruled out, they do not seem to materially affect the main results. Specifically, there
is a marked effect of IFRS adoption on analyst adjustments already in 2005.40
5.5 Subsets of firms
In this section, we focus on subsets of firm-year observations for which particular earnings
adjustments are more or less likely. The purpose is to investigate whether our main results are
concentrated in certain types of firms or driven by specific accounting items. The results are
reported in Table 7.
Our primary measure, the magnitude of analysts’ earnings adjustments, measures the net of
positive and negative adjustments. A potential concern with our main metric can be that we are
only able to measure the net of positive and negative adjustments that are done to reported
earnings. Consider a stylized example when negative adjustments of –10 and no positive
adjustments are made in the pre-IFRS adoption period. Then, in the post-adoption period,
negative adjustments are −10 and positive adjustments are +5, that is, analysts make more
adjustments in the post-adoption period. However, the example would generate a net absolute
and the PostIFRSt dummy as a determinant of AnalystAdjustment similar to Equation (3). The results (not tabulated)
show that the effect is insignificant at conventional levels.
40
A test comparing only 2004 (local GAAP) to 2005 (IFRS), and thus excluding all other years, also yields a
significant decrease in absolute adjustments (the point estimate is −0.0062 with a t-statistic of −5.91).
31
earnings adjustment of 10 in the pre-adoption period and 5 in the post-adoption period, thus
indicating a decrease in earnings adjustments.
We note that the tests in the Section 4.4, based on the number of adjusted line-items, are
not subject to this concern. To probe the sensitivity of the main results to this issue in a different
way, we also rerun our main tests on a sample that excludes observations we believe have both a
high likelihood of positive adjustments and a constant likelihood of negative adjustments. Under
the premise that analysts exclude income increasing fair value remeasurements, we eliminate
firms in the financial, real estate and forestry industries (IAS 39, 40 and 41 during our sample
period). Column 1 of Table 7 reports the results after removing firm-years from these industries.
The qualitative result on PostIFRS remains compared to the full-sample results in Table 3; if
anything, the coefficient is slightly more negative. While this result is consistent with the
existence of positive earnings adjustments in these industries, the effect is not large enough to
meaningfully affect the results.
As discussed in Section 2.1 prior literature reports substantial cross-sectional variation in
how analysts make earnings adjustments; that is, there does not seem to be a template for these
adjustments. That literature notwithstanding, a systematic exclusion of items that are affected by
the adoption of IFRS could confound the interpretation of our findings. We believe the issue is
most acute for goodwill. Assume that most analysts under local GAAP exclude both goodwill
amortization (in countries where goodwill was amortized) and impairments, but only goodwill
impairments after IFRS adoption (since goodwill is no longer amortized). This treatment could
induce a decrease in the absolute magnitude of analyst adjustments (unless the post-IFRS
adoption goodwill impairments exceed previous amortization charges). To investigate this issue
empirically, we exclude all observations with decreases in goodwill (i.e., observations with non-
32
zero goodwill amortization and non-zero goodwill impairments, net of increases in goodwill).
The results reported in Column 2 of Table 7 are very similar to the results in Table 3, indicating
that our main results are not driven by analysts’ treatment of goodwill amortizations and
goodwill impairments induced by the requirements of IFRS.
Finally, we exclude all observations with non-zero special items (results in Column 3) and
all observations with non-zero extraordinary items (results in Column 4). The results are robust
to such sample changes, and we conclude that neither of these items on their own can explain our
findings.
5.6 Distribution of firm-years
In the main tests, the requirement that firms have at least one observation each in the preand post-IFRS periods means that some firms have unequal numbers of observations in the preand post-IFRS adoption periods, respectively. To check the sensitivity of our results to this
issue, we increase the required number of observations to at least three each in the pre- and postperiod. Results (not tabulated) are unaffected by this stricter sample inclusion criterion.
5.7 The effect of scaling by total assets
As mentioned in Section 3, we scale our main adjustment variable by total assets, following
Doyle et al. (2003), Heflin and Hsu (2008) and Kolev et al. (2008). We address the concern that
the scaler itself may be affected by the IFRS adoption using 2004 data, where total assets are
available under both IFRS and local GAAP for the same sample firms. 41 We collect 2004 IFRS
total assets from Worldscope Restated Time-Series Data provided by Datastream. We also
collect local GAAP information for 2004 from Worldscope to ensure consistency. Holding the
41
As part of the IFRS transition firms were required to provide “as if” IFRS numbers for the fiscal year 2004 as part
of their 2005 annual reports. Consequently, there exist both local GAAP numbers (from the 2004 annual report)
and IFRS numbers (from the 2005 annual report) for year 2004. We note that while we thus have a scaler defined
under each system (GAAP vs. IFRS), we cannot use this setting as our main setting, since analysts in 2004 did not
have access to the 2004 IFRS figures for firms that mandatorily adopted IFRS in 2005.
33
sample constant, we scale the EPS adjustments for 2004 by total assets per share under IFRS
and, separately, under local GAAP. The distribution of the IFRS-scaled adjustments (not
tabulated) is similar to the distribution of the GAAP-scaled adjustments. The difference between
IFRS- and GAAP-asset-scaled adjustments is very small, with a mean (median) of −0.0002769
(−0.000000448). These differences are are also small relative to the difference in mean (median)
adjustments between IFRS and local GAAP, as shown in Table 2. We conclude that any IFRS
effect in the scaler, and hence the effect of over-time changes in the scaler on our main result, is
minor.
6.
Summary and discussion
In this study, we investigate the magnitude of analysts’ adjustments to reported earnings
surrounding a change in accounting regime, specifically the large-scale adoption of IFRS in
Europe. We view the magnitude of analyst adjustments as a summary indicator of how analysts
process earnings information produced under a set of accounting standards; more specifically,
we view them as an inverse indicator of how analysts perceive the quality of reported earnings.
While to our knowledge this interpretation has not been used explicitly in prior research, we
believe there is support for it in the analyst adjustment literature. First, studies on US data has
documented that analyst-adjusted earnings have properties consistent with high earnings quality,
both in terms of stock market reactions and in terms of valuation-relevant properties, such as
persistence and other earnings attributes.
Second, interview studies show that analysts
themselves motivate their adjustments as improvements along multiple dimensions of earnings
quality.
We find that analysts’ adjustments to reported earnings decrease in magnitude subsequent
to the mandatory adoption of IFRS in Europe. The effect is economically and statistically
34
significant, and it is robust to research design choices, such as estimation method and inclusion
of various control variables. We separately investigate earnings adjustments for voluntary IFRS
adopters. We find a similar decrease in analysts’ adjustments when firms voluntarily adopt IFRS
in years prior to 2005, but we find no additional effect in 2005. The finding indicates that
potential confounding effects in 2005 are unlikely to drive the main results for mandatory
adopters. To probe this issue further, we perform a difference-in-difference analysis with a
matched sample of US firms and find no 2005 effect on analyst adjustments for the US firms.
We further investigate the IFRS effect on the number of analyst adjustments. Similar to
other studies on analyst adjustments we do not have access to individual line-item adjustments,
and therefore develop a statistical methodology to estimate the number of analyst adjustments.
We believe this is a methodological contribution; substantively, the approach confirms that
analysts make significantly fewer adjustments after firms have adopted IFRS.
In summary, we view our evidence as consistent with financial analysts perceiving IFRS
earnings to be of higher quality than prior domestic-GAAP earnings. Further cross-sectional
results also support this interpretation: the decrease in earnings adjustments is more pronounced
for firms with poorer earnings quality (pre-IFRS), in countries with high legal enforcement and
in countries with large distance between local GAAP and IFRS. In additional tests we attempt to
distinguish between comparability and general earnings quality effects, and results indicate that
the decrease in analyst adjustments is not merely an effect of financial reports being more
comparable subsequent to the adoption of one common accounting regime.
Overall, we believe the study contributes to the earnings quality literature by explicitly
linking observable adjustments to reported earnings to a notion of perceived quality by an
influential and sophisticated user group. We further believe that our results on how financial
35
analysts process earnings information under local GAAP and IFRS, respectively, contribute to
the current debate on the consequences of the IFRS adoption in Europe. We do not claim that
we can settle this debate, however. Rather, we adopt the view expressed in Dechow et al. (2010)
that earnings quality is most meaningfully defined through a specific user’s perspective and in a
specific decision-making context. We view financial analysts and their earnings adjustments as
an interesting setting to study questions about earnings quality.
36
Appendix: IFRS adoption effects on earnings quality and other outcome variables
There is a large literature on how IFRS adoption affects earnings quality (defined in
various ways) and capital market outcomes.
Results are not consistent; for example,
Brüggemann et al.’s (2013, Table 1) review of nine studies that investigate various earnings
quality measures (value relevance, abnormal accruals, earnings persistence, the association
between current period earnings and future cash flows) lists three studies that find no IFRS
effect, three studies that find an improvement after IFRS adoption, two studies that find a
deterioration, and one study finding that the IFRS effect depends on which accounting property
is investigated. 42
There are also differences in findings from samples of voluntary adopters versus mandatory
adopters, holding the measure of earnings quality constant. For example, Barth et al. (2008) find
that voluntary adopters exhibit decreased income smoothing and increased timeliness of loss
recognition following IFRS adoption, whereas Ahmed et al. (2013) conclude the opposite for
mandatory adopters. Following arguments in Daske et al. (2008), Ahmed et al. attribute the
opposite results to voluntary adopters having stronger incentives to increase reporting quality
than mandatory adopters. Similarly, Christensen et al. (2015) conclude that the IFRS accounting
quality effect (defined as earnings management, timely loss recognition, and value relevance) is
confined to voluntary adopters.
In principle, better earnings quality might also be achieved with a consistent application of
a common set of accounting standards. Specifically, from a decision usefulness perspective
accounting comparability is a desirable quality dimension. Studies that explicitly focus on the
comparability aspect of IFRS, however, also arrive at different conclusions. For example, Yip
42
The nine studies are Aharony et al. (2010), Callao and Jarne (2010), Lang et al. (2010), Wu and Zhang (2010),
Atwood et al. (2011), Yip and Young (2012), Ahmed et al. (2013), Barth et al. (2014) and Bhat et al. (2014).
37
and Young (2012) conclude that mandatory IFRS adoption improves cross-country information
comparability, whereas Cascino and Gassen (2015) conclude that any comparability effects are
marginal at best, because of firm-level heterogeneity in IFRS compliance.
Research also shows that implementation choices and variation in enforcement affect the
the extent to which IFRS adoption influences financial reporting outcomes. For example, Kvaal
and Nobes (2010), Glaum et al. (2013) and Verriest et al. (2013) document both substantial
variation in IFRS policy choices and (non-)compliance.
Such implementation effects are
determined by both firm-level variables and incentives and country-level variables such as legal
enforcement (see Pope and McLeay 2011 for a more detailed discussion).
Capital market outcomes of IFRS adoption also tend to depend on country- or firm-specific
factors. For example, Li (2010) finds that IFRS adoption leads to a lower cost of equity capital
for mandatory adopters, but only in countries with a strong legal enforcement. Daske et al.
(2008) document a role for enforcement when investigating market liquidity, cost of capital, and
Tobin’s q around IFRS adoptions, and report that capital market effects are stronger for
voluntary than mandatory adopters. Christensen et al. (2013) conclude that the mandatory
change to IFRS had little effect on market liquidity, and that concurrent changes in enforcement
are at least as important. Barth and Israeli (2013) discuss this evidence and argue that both IFRS
adoption and enforcement are important.43
To our knowledge there are no studies investigating analyst adjustments in the context of
changes in accounting standards (neither in general nor specifically for IFRS). There are,
43
There is also a growing literature investigating the existence and magnitude of various other IFRS adoption
effects, more or less directly linked to capital markets. Examples include foreign mutual fund ownership (DeFond et
al. 2011), stock exchange listings (Han and He 2011), the US investor home bias (Khurana and Michas 2011),
institutional investment decisions (Florou and Pope 2012), dual-class share voting premia (Hong 2013), stock crash
risk (DeFond et al. 2015), initial public offerings (Hong et al. 2014), and international portfolio holdings (Yu and
Wahid 2014).
38
however, IFRS transition studies that focus on analyst forecast errors and forecast dispersion
(e.g., Byard et al. 2011, Tan et al. 2011, Horton et al. 2013). The empirical results are somewhat
mixed. Generally, forecast accuracy appears to improve for voluntary IFRS adopters (e.g.,
Ashbaugh and Pincus 2001, Ernstberger et al. 2008), but for mandatory adopters the effect
depends on analyst-specific, firm-specific and/or country-specific factors. Horton et al. (2013)
document an overall decrease in forecast errors after the mandatory adoption of IFRS in several
countries. Tan et al. (2011), however, find no IFRS effect on forecast accuracy for local analysts
(domiciled in the same country as the firm they follow), and they conclude that improvements in
forecast accuracy are attributable to foreign analysts (domiciled in another country). Similarly,
Byard et al. (2011) find no general IFRS effect, but there is an effect in countries with high
distance between IFRS and local GAAP and high legal enforcement. While related to our topic
in the sense that these studies build on analyst data, forecast error and forecast dispersion are
conceptually and empirically distinct from our measure of analyst adjustments to earnings (we
investigate this issue in detail in Section 5.1).
39
REFERENCES
Aharony, J., R. Barniv and H. Falk. 2010. The impact of mandatory IFRS adoption on equity
valuation of accounting numbers for security investors in the EU. European Accounting
Review 19: 535–578.
Ahmed, A., M. Neel, and D. Wang. 2013. Does Mandatory Adoption of IFRS Improve
Accounting Quality? Preliminary Evidence. Contemporary Accounting Research 30: 13441372.
Andersson, P. and N. Hellman. 2007. Does Pro Forma Reporting Bias Analyst Forecasts?
European Accounting Review 16: 277-298.
Ashbaugh, H., and M. Pincus. 2001. Domestic Accounting Standards, International Accounting
Standards, and the Predictability of Earnings. Journal of Accounting Research 39: 417-434.
Atwood, T., M. Drake, J. Myers, and L. Myers. 2011. Do Earnings Reported under IFRS Tell
Us More About Future Earnings and Cash Flows? Journal of Accounting and Public Policy
30: 103-121.
Bae, K., H. Tan, and M. Welker. 2008. International GAAP Differences: The Impact on
Foreign Analysts. The Accounting Review 83: 593-628.
Baik, B., D. Farber, and K. Petroni. 2009. Analysts’ Incentives and Street Earnings. Journal of
Accounting Research 47: 45-69.
Barker, R., and S. Imam. 2008. Analysts’ Perception of “Earnings’ Quality.” Accounting and
Business Research 38: 313-329.
Barth, M., W. Landsman and M. Lang. 2008. International Accounting Standards and
Accounting Quality. Journal of Accounting Research 46: 467-498.
Barth, M. and D. Israeli. 2013. Disentangling mandatory IFRS reporting and changes in
enforcement. Journal of Accounting and Economics 56: 178–188.
Barth, M., W. Landsman, D. Young and Z. Zhuang. 2014. Relevance of Differences between
Net Income based on IFRS and Domestic Standards for European Firms. Journal of
Business Finance and Accounting 41: 297-327.
Beauducel, A. and P. Yorck Herzberg. 2006. On the Performance of Maximum Likelihood
Versus Means and Variance Adjusted Weighted Least Squares Estimation in CFA.
Structural Equation Modeling: A Multidisciplinary Journal 13: 186-203.
Bhat, G., J. Callen and D. Segal. 2014. Credit risk and IFRS: The case of credit default swaps.
Journal of Accounting, Auditing & Finance 29: 129-162.
Bhattacharya, N., E. Black, T. Christensen and C. Larson. 2003. Assessing the Relative
Informativeness and Permanence of Pro Forma Earnings and GAAP Operating Earnings.
Journal of Accounting and Economics 36: 285-319.
Bradshaw, M. 2011. A Discussion of “Do Managers Use Earnings Guidance to Influence Street
Earnings Exclusions?”. Review of Accounting Studies 16: 528-538.
Bradshaw, M., and R. Sloan. 2002. GAAP versus the Street: An Empirical Assessment of Two
Alternative Definitions of Earnings. Journal of Accounting Research 40: 41-66.
Brown, L., and K. Sivakumar. 2003. Comparing the Value Relevance of Two Operating
Income Measures. Review of Accounting Studies 8: 561–572.
40
Brown, P., J. Preiato and A. Tarca. 2014. Measuring Country Differences in Enforcement of
Accounting Standards: An Audit and Enforcement Proxy. Journal of Business Finance and
Accounting 41: 1-52.
Brüggemann, U., J-M. Hitz and T. Sellhorn. 2013. Intended and Unintended Consequences of
Mandatory IFRS Adoption: A Review of Extant Evidence and Suggestions for Future
Research. European Accounting Review 22: 1-37.
Byard, D., Y. Li and Y. Yu. 2011. The Effect of Mandatory IFRS Adoption on Financial
Analysts’ Information Environment. Journal of Accounting Research 49: 69-96.
Callao, S. and J. Jarne. 2010. Have IFRS affected earnings management in the European
Union? Accounting in Europe 7:159–189.
Cascino, S., and J. Gassen. 2015. What Drives the Comparability Effect of Mandatory IFRS
Adoption? Review of Accounting Studies 20: 242-282
Choi, Y-S., S. Lin, M. Walker and S. Young. 2007. Disagreement over the Persistence of
Earnings Components: Evidence on the Properties of Management-Specific Adjustments to
GAAP Earnings. Review of Accounting Studies 12: 595-622
Christensen, T., K. Merkley, J. Tucker and S. Venkataraman. 2011. Do Managers Use Earnings
Guidance to Influence Street Earnings Exclusions? Review of Accounting Studies 16: 501527.
Christensen, H., L. Hail and C. Leuz. 2013. Mandatory IFRS Reporting and Changes in
Enforcement. Journal of Accounting and Economics 56: 147-177.
Christensen, H. E. Lee, M. Walker and C. Zeng. 2015. Incentives or Standards: What
Determines Accounting Quality Changes around IFRS Adoption? European Accounting
Review 24: 31-61.
Cohen, D., A. Dey and T. Lys. 2008. Real and Accruals-Based Earnings Management in the
Pre- and Post-Sarbanes-Oxley Periods. The Accounting Review 83: 757-787.
Daske, H., L. Hail, C. Leuz and R. Verdi. 2008. Mandatory IFRS Reporting Around the World:
Early Evidence on the Economic Consequences. Journal of Accounting Research 46: 10851142.
Dechow, P., and I. Dichev. 2002. The Quality of Accruals and Earnings: The Role of Accrual
Estimation Errors. The Accounting Review 77: 35-59.
Dechow, P., W. Ge and C. Schrand. 2010. Understanding Earnings Quality: A Review of the
Proxies, Their Determinants and Their Consequences. Journal of Accounting and Economics
50: 344-401
DeFond, M., X. Hu, M. Hung and S. Li. 2011. The Impact of Mandatory IFRS Adoption on
Foreign Mutual Fund Ownership: The Role of Comparability. Journal of Accounting and
Economics 51: 240-258.
DeFond, M., M. Hung, S. Li and Y. Li. 2015. Does Mandatory IFRS Adoption Affect Crash
Risk? The Accounting Review 90: 265-299
Doyle, J., R. Lundholm and M. Soliman. 2003. The Predictive Value of Expenses Excluded
from Pro Forma Earnings. Review of Accounting Studies 8: 145-174.
Doyle, J., J. Jennings and M. Soliman. 2013. Do Managers Define Non-GAAP Earnings to
Meet or Beat Analyst Forecasts? Journal of Accounting and Economics 56: 40-56.
Ecker, F., J. Francis, P. Olsson and K. Schipper. 2013. Estimation Sample Selection for
Discretionary Accruals Models. Journal of Accounting and Economics 56: 190-211.
41
Entwistle, G., G. Feltham and C. Mbagwu. 2006. Financial Reporting Regulation and the
Reporting of Pro Forma Earnings. Accounting Horizons 20: 39–55.
European Commision Regulation No. 1606/2002. Eur-lex.Europa.eu. Official Journal of the
European Communities. September 11, 2002. L243.
Florou, A., and P. Pope. 2012. Mandatory IFRS Adoption and Institutional Investment
Decisions. The Accounting Review 87: 1993-2025.
Glaum, M., P. Schmidt, D. Street and S. Vogel. 2013. Compliance with IFRS 3 and IAS36required disclosures across 17 European countries: company- and country-level determinants.
Accounting and Business Research 43: 163–204.
Graham, C., M. Cannice and T. Sayre. 2002. Analyzing Financial Analysts: What They Look
for in Financial Reports and How They Determine Earnings’ Quality. Journal of
Management Research 2: 63-72.
Gu, Z., and T. Chen. 2004. Analysts’ Treatment of Nonrecurring Items in Street Earnings.
Journal of Accounting and Economics 38: 129-170.
Han, F., and H. He. 2011. The Impact of Mandatory IFRS Adoption on Stock Exchange
Listings: International Evidence. Academy of Accounting and Financial Studies Journal 15:
31-40.
Heflin, F., and C. Hsu. 2008. The Impact of the SEC’s Regulation of Non-GAAP Disclosures.
Journal of Accounting and Economics 46: 349-365.
Heflin, F., C. Hsu and Q. Jin. 2015. Accounting Conservatism and Street Earnings. Review of
Accounting Studies 20: 674-709.
Hjelstrom, A., T. Hjelstrom and E. Sjogren. 2014. An Investigation of Capital Market Actors’
Use of Financial Reports. Confederation of Swedish Enterprise.
Hong, H. 2013. Does Mandatory Adoption of International Financial Reporting Standards
Decrease the Voting Premium for Dual-Class Shares? The Accounting Review 88: 12891325.
Hong, H., M. Hung and G. Lobo. 2014. The Impact of Mandatory IFRS Adoption on IPOs in
Global Capital Markets. The Accounting Review 89: 1365-1397.
Horton, J., G. Serafeim and I. Serafeim. 2013. Does Mandatory IFRS Adoption Improve the
Information Environment? Contemporary Accounting Research 30: 388-423.
Isidro, H., and A. Marques. 2014. The Role of Institutional and Economic Forces in the
Strategic Use of Non-GAAP Disclosures to Beat Earnings Benchmarks. European
Accounting Review 24: 95-128.
Jones, J. 1991. Earnings Management during Import Relief Investigations. Journal of
Accounting Research 29: 193-228.
Khurana, I., and P. Michas. 2011. Mandatory IFRS Adoption and the US Home Bias.
Accounting Horizon 25: 729-753.
Kolev, K., C. Marquardt and S. McVay. 2008. SEC Scrutiny and the Evolution of Non-GAAP
Reporting. The Accounting Review 83: 157-184.
Kvaal, E., and C. Nobes. 2010. International differences in IFRS policy choice: a research note.
Accounting and Business Research 40: 173–187.
Lang, M., M. Maffett and E. Owens. 2010. Earnings Co-movement and Accounting
Comparability: The Effects of Mandatory IFRS Adoption, Working paper
42
Li, S. 2010. Does Mandatory Adoption of International Financial Reporting Standards in the
European Union Reduce the Cost of Equity Capital? The Accounting Review 85: 607-636.
Lougee, B., and C. Marquardt. 2004. Earnings Informativeness and Strategic Disclosure: An
Empirical Examination of “Pro Forma” Earnings. The Accounting Review 79: 769-795.
Marques, A. 2006. SEC Interventions and the Frequency and Usefulness of Non-GAAP
Financial Measures. Review of Accounting Studies 11: 549-574.
McNichols, M. 2002. Discussion of “The Quality of Accruals and Earnings: The Role of
Accrual Estimation Errors”. The Accounting Review 77 (Supplement): 61-69.
Muthen, B. 1984. A general structural equation model with dichotomous, ordered categorical,
and continuous latent variable indicators. Psychometrika 49: 115–132.
Nobes, C. 2001. GAAP 2001 – A Survey of National Accounting Rules Benchmarked against
International Accounting Standards. International Forum on Accountancy Development
(IFAD).
Pope, P., and S. McLeay. 2011. The European IFRS experiment: objectives, research
challenges and some early evidence. Accounting and Business Research 41: 233–266.
Tan, H., S. Wang and M. Welker. 2011. Analyst Following and Forecast Accuracy After
Mandated IFRS Adoptions. Journal of Accounting Research 49: 1307-1357.
Timm, N. 2002. Applied multivariate analysis. Springer, New York.
Verriest, A., A. Gaeremynck and D. Thornton. 2013. The Impact of Corporate Governance on
IFRS Adoption Choices. European Accounting Review 22: 39-77.
Wang, J., and X. Wang. 2012. Structural equation modelling: applications using Mplus. Wiley
and Sons, West Sussex.
Wu, J., and I. Zhang. 2010. Accounting Integration and Comparability: Evidence from Relative
Performance Evaluation around IFRS Adoption. Working paper.
Yip, R.,, and D. Young. 2012. Does Mandatory IFRS Adoption Improve Information
Comparability? The Accounting Review 87: 1767-1789.
Yu, G., and A. Wahid. 2014. Accounting Standards and International Portfolio Holdings. The
Accounting Review 89: 1895-1930.
43
Table 1
Sample Counts per Country
Country
Austria
Belgium
Czech Republic
Germany
Denmark
Spain
Finland
France
Great Britain
Greece
Hungary
Ireland
Italy
Netherlands
Norway
Poland
Portugal
Sweden
Slovenia
Total
Firm years
26
532
14
618
420
841
823
2,605
5,577
568
11
225
1,465
717
733
237
208
1,091
37
16,748
# Firms
3
53
1
73
45
74
75
259
608
65
1
21
154
67
82
24
19
116
4
1,744
Sample description: The sample of mandatory adopters include observations from
1999-2012. We require firms to have observations in both the pre- and post-IFRS
periods and we require firms to be from countries with sufficient data to estimate
measures of legal enforcement and accounting data. The final sample contains
16,748 firm-year observations originating from 1,744 analyst-followed firms from
19 countries.
44
Table 2
Descriptive Statistics
Panel A: Analyst Adjustments in Sample of Mandatory Adopters (n=16,748)
Mean
Std. dev.
Q1
Median
Q3
Total sample
0.0174
0.0447
0.0001
0.0015
0.0134
Pre-IFRS period
Post-IFRS period
0.0188
0.0163
0.0512
0.0392
0.0001
0.0001
0.0022
0.0011
0.0137
0.0132
Difference
Significance of difference
-0.0025
0.0004
-0.0010
0.0204
Panel B: Analyst Adjustments in Sample of Voluntary Adopters (n=1,115)
Mean
Std. dev.
Q1
Median
Q3
Total sample
0.0117
0.0375
0.0000
0.0005
0.0060
Pre-IFRS period
Post-IFRS period
0.0187
0.0093
0.0524
0.0304
0.0001
0.0000
0.0023
0.0003
0.0120
0.0040
Difference
Significance of difference
-0.0095
0.0002
-0.0020
0.0001
Panel C: Descriptive Statistics of Other Variables
Variable
AbsDiscrAcc
Enforcement (Factor)
Accounting Distance (Factor)
Mean
Std. dev.
Q1
Median
Q3
0.0844
0.0842
-0.0215
0.0783
1.5762
0.3346
0.0414
-0.8250
-0.2830
0.0631
0.7200
-0.0680
0.0998
1.1270
0.2460
Panel A reports descriptive statistics for AnalystAdjustments for mandatory adopters; for the full sample period and for the preand post-IFRS periods, respectively. Panel B resports descriptive statistics for AnalystAdjustments for the sample of voluntary
adopters. AnalystAdjustments is the absolute difference between reported earnings per share from Compustat Global and analyst
adjusted earnings per share (EPS Actual) from IBES international summary file, scaled by total assets per share. Panel C reports
summary data for AbsDiscrAcc (absolute discretionary accruals from a modified Jones model, estimated in the pre-IFRS period),
Enforcement (from a confirmatory factor analysis based on categorical variables measured in 2005 as described in Section 3), and
AccountingDistance (from a confirmatory factor analysis based on accounting standard differences between local accounting
standards and IFRS as described in Section 3).
45
Table 3
IFRS Effect on the Magnitude of Analysts’ Earnings Adjustments (Mandatory Adopters)
Variable
Exp.
Sign
PostIFRS
(-)
Crisis
(+)
Time
(+)
Country-Fixed Effects
Firm-Fixed Effects
Adj. R 2
# Obs.
(1)
(2)
(3)
(4)
(5)
(6)
-0.0020
-2.91
-0.0031
-4.26
-0.0081
-6.22
-0.0020
-2.97
-0.0030
-4.27
-0.0081
-6.62
0.0050
4.90
0.0045
4.33
0.049
5.09
0.0044
4.54
0.0008
4.63
Yes
0.0308
16,748
Yes
0.0008
5.08
Yes
0.0322
16,748
0.0334
16,748
Yes
Yes
Yes
0.1699
16,748
0.1713
16,748
0.1727
16,748
The table reports coefficient estimates obtained from regressions of AnalystAdjustments on PostIFRS, Crisis and Time for
mandatory IFRS adopters. AnalystAdjustments is the absolute difference between reported earnings per share from Compustat
Global and analyst-adjusted earnings per share (EPS Actual) from IBES international summary file scaled by total assets.
PostIFRS is an indicator variable that takes the value 0 (1) for pre-IFRS (post-IFRS) observations. The transition year is 2005 for
all firms included in the sample. Crisis is a country- and year-specific variable that takes the value of 1 if GDP growth is
negative and zero otherwise. Time is equal to the difference between the year of the observation and 1999. Columns 1-3 report
results from regressions using country-fixed effects and columns 4-6 report results from regressions using firm-fixed effects.
46
Table 4
IFRS Effect on the Magnitude of Analysts’ Earnings Adjustments (Voluntary Adopters)
Variable
PostIFRS (firm-specific)
(1)
(2)
(3)
(4)
-0.0090
-3.60
-0.0090
-3.57
-0.0099
-2.87
-0.0101
-2.93
0.0000
0.00
-0.0001
-0.03
0.0003
0.09
-0.0002
-0.05
0.0001
0.37
-0.0002
-0.30
-0.0009
-1.55
0.0031
0.74
0.0020
0.48
Crisis
Time
Post2005
Firm-Fixed Effects
2
Adj. R
# Obs.
(5)
Yes
Yes
Yes
Yes
Yes
0.1506
1,115
0.1505
1,115
0.1506
1,115
0.1510
1,115
0.1438
1,115
The table reports the coefficient estimate obtained from regressions of AnalystAdjustments on PostIFRS (firm-specific), Crisis,
Time and Post2005. AnalystAdjustments is the absolute difference between reported earnings per share from Compustat Global
and analyst-adjusted Earnings per share (EPS Actual) from IBES international summary file scaled by total assets. PostIFRS
(firm-specific) is an indicator variable that takes the value 0 (1) for pre-IFRS (post-IFRS) observations based on the specific
IFRS transition year for each firm. Crisis is a country- and year-specific variable that takes the value of 1 if GDP growth is
negative and zero otherwise. Time is equal to the difference between the year of the observation and 1999. Post2005 is an
indicator variable that takes the value 0 (1) for observations before 2005 (from 2005 and thereafter). All regressions are
estimated using firm-fixed effects.
47
Table 5
IFRS Effect on the Magnitude of Analysts’ Earnings Adjustments for
Mandatory Adopters Compared to a US Benchmark Sample
Variable
(1)
(2)
(3)
Post2005
0.0040
4.89
-0.0010
-0.85
-0.0006
-0.40
IFRSAdopter*Post2005
-0.0060
-5.28
-0.0058
-5.09
-0.0073
-3.58
0.0117
13.97
0.0195
16.09
Crisis
IFRSAdopter*Crisis
-0.0149
-8.92
Time
0.0004
2.83
IFRSAdopter*Time
Firm-Fixed Effects
Adj. R 2
# Obs.
0.0000
0.16
0.0008
2.77
Yes
Yes
Yes
0.1934
31,852
0.1992
31,852
0.2015
31,852
The table reports the coefficient estimates from difference-in-difference regressions adding a
control sample of matched US firms. The sample contains 31,852 firm year observations. The
coefficient estimates are from regressions of AnalystAdjustments on Post2005, Crisis, Time all
with and without interactions with IFRSAdopter. AnalystAdjustments is equal to the absolute
difference between reported Earnings per share from Compustat Global and analyst adjusted
Earnings per share (EPS Actual) from IBES international summary file scaled by total assets.
Post2005 is an indicator variable that takes the value of 0 (1) for observations before 2005
(from 2005 and thereafter). Crisis is a country- and year-specific variable that takes the value of
1 if GDP growth is negative and zero otherwise. Time is equal to the difference between the
year of the observation and 1999. IFRSAdopter is an indicator variable that takes the value of 0
(1) for US firms (for IFRS firms). All regressions are estimated using firm-fixed effects.
48
Table 6
Cross-sectional Variation in the IFRS Effect on the Magnitude of Analysts’ Earnings
Adjustments (Mandatory Adopters)
Variable
Exp.
Sign
PostIFRS
(1)
(2)
(3)
(-)
-0.0068
-4.36
-0.0082
-6.71
-0.0068
-4.36
Crisis
(+)
0.0028
2.68
0.0043
4.45
0.0028
2.68
Time
(+)
0.0010
5.60
0.0008
5.11
0.0010
5.60
Interaction of PostIFRS with:
Pre-IFRS AbsDiscrAcc
(-)
-0.0506
-5.45
Enforcement
(-)
AccountingDistance
(-)
-0.0012
-2.84
-0.0051
-2.53
Firm-Fixed Effects
Adj. R 2
# Obs.
Yes
Yes
Yes
0.2527
14,286
0.1802
16,748
0.1801
16,748
The table reports the coefficient estimate obtained from regressions of AnalystAdjustments on PostIFRS,
Crisis, Time and interactions between PostIFRS and three cross-sectional determinants for the IFRS
effects. The cross-sectional determinants are absolute discretionary accruals, AbsDiscRacc, from a
modified Jones model, Enforcement, from a confirmatory factor analysis based on three categorical
variables, and AccountingDistance from a confirmatory factor analysis based on five accounting standards.
AnalystAdjustments is equal to the absolute difference between reported Earnings per share from
Compustat Global and analyst adjusted Earnings per share (EPS Actual) from IBES international summary
file scaled by total assets. PostIFRS is an indicator variable that takes the value of 0 (1) for pre-IFRS (postIFRS) observations. The transition year is 2005 for all firms included in the sample. Crisis is a countryand year-specific variable that takes the value of 1 if GDP growth is negative and zero otherwise. Time is
equal to the difference between the year of the observation and 1999. All regressions are estimated using
firm-fixed effects.
49
Table 7
IFRS Effect on the Magnitude of Analysts’ Earnings Adjustments
in Sub-Samples of Mandatory Adopters
Excluding
Excluding
observations with
observations in real
non-zero goodwill
estate, financial and
amortization and
forestry industries
impairments
Variable
Exp.
Sign
PostIFRS
Excluding
observations with
special items
Excluding
observations with
extraordinary items
(1)
(2)
(3)
(4)
(-)
-0.0112
-8.25
-0.0086
-6.81
-0.0103
-6.83
-0.0079
-5.58
Crisis
(+)
0.0030
2.80
0.0045
4.49
0.0047
3.98
0.0044
3.88
Time
(+)
0.0001
5.52
0.0009
5.20
0.0011
5.49
0.0008
4.33
Yes
Yes
Yes
Yes
0.1522
14,296
0.1731
15,823
0.1637
13,263
0.1656
13,140
Firm-Fixed Effects
Adj. R 2
# Obs.
The table reports coefficient estimates from regressions of AnalystAdjustments on PostIFRS, Crisis and Time using four subsamples. The first sub-sample excludes firm-year observations from firms in the real estate, financial and forestry industries.
The second sub-sample excludes observations with non-zero goodwill amortizations or impairments. The third sub-sample
excludes observations with non-zero special items and the fourth sub-sample excludes observations with non-zero
extraordinary items. AnalystAdjustments is the absolute difference between reported Earnings per share from Compustat
Global and analyst-adjusted earnings per share (EPS Actual) from IBES international summary file scaled by total assets.
PostIFRS is an indicator variable that takes the value 0 (1) for pre-IFRS (post-IFRS) observations. The transition year is 2005
for all firms included in the sample. Crisis is a country- and year-specific variable that takes the value 1 if GDP growth is
negative and zero otherwise. Time is equal to the difference between the year of the observation and 1999. All regressions are
estimated using firm-fixed effects.
50