empirical accounting research design for ph.d. students

Empirical Accounting Research Design for Ph. D. StudentsAuthor(s): William R. Kinney, Jr.Source: The Accounting Review, Vol. 61, No. 2 (Apr., 1986), pp. 338-350Published by: American Accounting AssociationStable URL: http://www.jstor.org/stable/247264 .

Accessed: 09/05/2014 16:35

Your use of the JSTOR archive indicates your acceptance of the Terms & Conditions of Use, available at .http://www.jstor.org/page/info/about/policies/terms.jsp

.JSTOR is a not-for-profit service that helps scholars, researchers, and students discover, use, and build upon a wide range ofcontent in a trusted digital archive. We use information technology and tools to increase productivity and facilitate new formsof scholarship. For more information about JSTOR, please contact [email protected].

.

American Accounting Association is collaborating with JSTOR to digitize, preserve and extend access to TheAccounting Review.

http://www.jstor.org

This content downloaded from 169.229.32.138 on Fri, 9 May 2014 16:35:44 PMAll use subject to JSTOR Terms and Conditions

http://www.jstor.org/action/showPublisher?publisherCode=aaasoc

http://www.jstor.org/stable/247264?origin=JSTOR-pdf

http://www.jstor.org/page/info/about/policies/terms.jsp


THE ACCOUNTING REVIEW Vol. LXI, No. 2 April 1986

EDUCATION RESEARCH

Frank H. Selto, Editor

Empirical Accounting Research Design

For Ph.D. Students

William R. Kinney, Jr.

ABSTRACT: This paper discusses an approach to introducing empirical accounting research design to Ph.D. students. The approach includes a framework for evaluating accounting experiments as well as studies based on passive observation of subjects or data. Alternative methods of isolating the effect of the "independent" variable of interest from effects of prior- to-the-study-period variables and contemporaneous variables are discussed along with the advantages and limitations of each method. Also discussed is the relationship between type I and type 11 error risks, sample size, and research design. The importance of research design, including theory development and means for mitigating the effects of extraneous variables, is emphasized as perhaps the only practical way to achieve research objectives in empirical research in accounting.

A FREQUENTLY encountered problem in accounting Ph.D. programs is that first-year students do not have

background in empirical research in accounting. Few B.B.A., M.B.A. or M.Acc. programs include courses in empirical research and many students have not seri- ously considered its nature. Yet, such an introduction is necessary if Ph.D students are to efficiently relate other courses to substantive problems in accounting and be able to take full advantage of accounting workshops.

The purpose of this paper is to show how a basic framework for evaluating empirical research in accounting can be obtained in a short introduction. This can be done at the start of the first term course and provides a context for further work in philosophy of science and statistical design as well as substantive areas of accounting.

The approach is generic-it is not tied to an area of accounting and doesn't depend on prior knowledge of a particular para- digm.'

' Illustrations and extensions from applied areas of accounting are also helpful. Good sources for financial accounting are Ball and Foster [1982], Lev and Ohlson [1982], and Abdel-khalik and Ajinkya [1979]. Good sources for behavioral work are Ashton [1982] and Libby [1981].

I would like to acknowledge the helpful comments and suggestions of Vic Bernard, Dan Collins, Grant Clowery, Bob Libby, Jerry Salamon and two anonymous reviewers. An earlier version of this paper was presented at the American Accounting Association's Doctoral Consor- tium in Toronto, Ontario, in August 1984.

William R. Kinney, Jr. is Price Water- house Auditing Professor at the Univer- sity of Michigan.

Manuscript received September 1984. Revisions received April 1985 and August 1985. Accepted September 1985.

338



Kinney 339

The generic approach focuses attention on the essence of scientific inquiry in accounting. Many of the problems faced by accounting experimenters who can man- ipulate some (but not all) of the levels of variables to be studied are similar to those faced by "passive observers" of the levels of all variables as set by Nature.2 Thus, the generic approach may help to avoid premature specialization [Boulding, 1956, p. 199].

Section I presents a definition of empirical accounting research and theory, hypothesis, and fact. It also defines "dependent," "independent," and prior and contemporaneous influence variables. Section II discusses alternative means for separating the effects of prior and contemporaneous influence variables from the independent variable(s), and in Section III the interrelationships among significance, power, and research design are explored. Section IV gives a summary and conclusions.

I. A FRAMEWORK FOR EMPIRICAL RESEARCH IN ACCOUNTING

Research is a purposive activity and its purpose is to allow us to understand, predict, or control some aspect of the envi- ronment. Research will be defined here as the development and testing of new theories of 'how the world works' or refu- tation of widely held existing theories. For accounting research, the theories con- cern how the world works with respect to accounting practices. Watts and Zimmer- man [1984, p.1], state: "The objective of accounting theory is to explain and predict accounting practice." This positive, how- the-world-is approach is in contrast with the more traditional normative view that accounting "theory" is concerned with what accounting practices ought to be.

Empirical accounting research (broadly considered) addresses the question: "Does how we as a firm or as a society account

for things make a difference?"' Clearly, the accounting for items affecting tax pay- ments makes a difference in our individual and collective lives. But does the accounting for, say, depreciation in internal or external reports affect decisions within a business firm or affect stock prices? If it does, then the size of the effect and why it occurs are important follow-up questions. Additionally, the accounting researcher must separate the underlying economic event (or state) from the accounting report of the event. Thus, while a finance researcher may be concerned only with firm characteristics, the accounting researcher must also be concerned with the costs and benefits of alternative accounting reports of those characteristics.4

In essence, empirical research involves theory, hypothesis, andfact. "Facts" are states or events that are observable in the real world. A "theory" offers a tentative explanation of the relationship between or among groups of facts in general. "Hy- potheses" are predictions (or assertions) about the "facts" that will occur in a particular instance assuming that the theory is valid. Finally, observing "facts" consistent with the prediction or assertion

2 The problems are not identical. For example, while experimenters have the advantage of being able to specify the values of some variables, they also face the risk of choosing values that are too close together (or too far apart) to allow precise estimates of treatment effects or to allow generalization of conclusions to the real world.

3 Within this definition, relevant questions for auditing include, "Does how precisely we audit and report the state of a firm make a difference?" and, "How can audits of a given precision be conducted efficiently?" The first auditing question is related to the accounting question through the concept of materiality. Parallel questions involving the design of accounting systems also could be developed.

4Accounting professors may conduct research in finance, economics, behavioral science, or statistics. If the accounting question is not addressed, however, the accounting professor may face the disadvantage of being undertrained relative to other researchers. Also, he or she ignores a comparative advantage in the knowledge of accounting institutions and the sometimes subtle role of information.



340 The Accounting Review, April 1986

made in the hypothesis lends credibility to the theory.

Ordinarily, research begins with a real- world problem or question. One thinks about or studies the problem, reads about seemingly similar problems in other areas or disciplines such as economics, psy- chology, organizational behavior, or po- litical science. By immersing himself or herself in the problem, the researcher may, either by genius or by adapting a solution from another area, develop a general theory to explain relationships among facts [Simon, 1976, Chapter 7 and Boulding, 1956]. From this statement of the general relationship among facts, hypotheses about what should be observed in a particular situation can be derived. An experiment or passive observation study then can be designed to support or deny the hypotheses.

For example, suppose it is observed that a stock price increase usually follows the announcement that a firm has changed from straight-line to accelerated depreciation. Why should a mere bookkeep- ing change seem to lead to an increase in firms' values? An explanation might be that market participants believe that events leading to such an accounting change also typically lead to better prospects for the firm in the future. With development and elaboration of such a theory, the researcher might develop a passive observation study of past changes or an experiment to test hypotheses based on the proposed explanation.

Theories are usually stated in terms of theoretical variables or "principals" while empirical measurement requires observable variables. The difference between the principal and real-world observable variables presents difficulties for accounting researchers since accounting mea- surements may be either surrogates for some underlying principal of interest or may be the principal itself. For example,

if firm "performance" is the theoretical principal and earnings is chosen as the surrogate measure of firm performance, then straight-line depreciation is a com- ponent of the surrogate.

As a surrogate, straight-line depreciation contains two sources of potential error that may require consideration by the researcher. One is the surrogation error due to the fact that straight-line depreciation does not "correctly" reflect the relevant performance of the firm for the purpose at hand. The other is application error due to mistakes or imprecision in applying straight-line depreciation.

On the other hand, in evaluating possible determinants of managerial behavior, audited earnings using straight-line depreciation may be specified in a contract and may serve as a principal. For example, if a manager is to receive a bonus or profit share of one percent of audited earnings, then audited earnings is the principal. Surrogation error, and any application error not detected and corrected by the auditor, is ignored for contract purposes. The same number used as a measure of firm performance will likely contain both surrogation and application error.5

To add credibility to a theory, one must not only be able to show hypothesis test results that are consistent with the theory's predictions, but also have a basis to rule out alternative explanations of the observed facts. This requires consideration of a reasonably comprehensive list of alternative explanations. Again, knowledge of related disciplines is useful in generating alternative explanations for accounting-related "facts." Some possible explanations can, of course, easily be ruled out as being of

5 Accounting systems designers and financial accounting standards setters can control the first type of measurement error, while auditors and auditing standards setters can control the second. Problems relating to the interaction of accounting and auditing standards setters, users, and auditors is, of course, a matter for accounting research.



Kinney 341

likely negligible effect, but others will require attention.

To be more specific, let Y denote the "dependent" variable to be understood, explained, or predicted. Variables caus- ing Y(or at least related to Y) can be clas- sified into three broad groups as follows:

X=the "independent" variable that the proposed theory states should effect Y,

Vs = prior-influence (prior-to-study period) factors that may affect Y, and

Zs= contemporaneous factors (other than X) that may affect Y.6

That is, Y=f(X, V,, V2, . ..,ZIZ2, ...

A common Yfor addressing an accounting question is the change in a firm's stock price. Others are a manager's act or decision. A common X is a change or difference in accounting method, whether by management's choice or by a regulatory directive. Prevalent Vs are the firm's prior period state variables such as profitability, leverage, liquidity, and size. For tests of theories about decision-making behavior of particular human subjects, relevant Vs often include the subject's personality traits, mathematical ability, education, training, age, firm association, and exper- ience.

The most common Z factor in accounting research studies involving stock prices is the market return (Rm). Another common group of Zs for external reporting and managerial performance studies is the unexpected portion of contemporaneous accounting measures for other firms or other divisions. Finally, since the accounting researcher is concerned with the effect of accounting reports, Zs may be underlying characteristics of the "true state" of the firm at the time of the study as measured by contemporaneous nonac- counting reports about the firm.

DISENTANGLING THE EFFECTS FROM VS AND ZS FROM THE EFFECT OF X

For simplicity, assume that X is measured at only two levels. Either the observed Yis from the "control" group that receives no "treatment" or from the treatment group that receives the treatment. Alter- natively, the two groups could simply be different on some relevant dimension (e.g., to test theories about accelerated depreciation, the control group might be defined as those firms that use straight- line and the treatment group as those that use accelerated).

Also for simplicity, assume that there is a single prior-influence factor Vthat effects Yand Vhas the same effect on Ywhether the subject is from the control or treatment group. Furthermore, there are no contemporaneous Zs that affect Y and the model determining Y is:

Yij=Bo+BX,+B2Vj+ ej,, (1)

where Yij is the value of the dependent variable for the "j"th subject in the "i"th treatment, Bo is the intercept for the control group, Xi is an indicator variable (zero for the control group and one for treatment), Bo + B1 is the intercept for the treatment group (that is, B1 is the effect of treatment), B2 is the regression coefficient relating Vto Y, and eij is a random error term. The eij term will include the effects of other Vs and Zs that are here assumed to be negligible and randomly distributed between the two groups, and eij is assumed to have expectation zero and be uncorre- lated with either X or V.

For the simple model of equation 1, a plot of the expected values of Y given V for both groups will be parallel lines with possibly different intercepts. The difference in intercepts is the effect of the treatment (B1). Figure 1 shows the components

6 Some Zs may be expectations, at the time of the study, of still future values of X, Y, V, and other Zs.




FIGURE 1

Y VALUES FOR NONEQUIVALENT GROUPS UNDER ANOVA, ANCOVA, AND MATCHING

y

I ~~~~~~~~~~~~Y=00+ X+02V

ANOVA X

;

/- | ~~~NCOVA and Matching V

~~~~~~~~~~I I

l I _~~~~~~ I I I I

V. V Vs

Matches

of equation 1 along with ellipses that ap- proximate the locus of members of the two groups.

An experimenter may ignore V and may randomly assign subjects to groups. On average, the groups will be equivalent on V. For small samples, however, there is nontrivial risk that such a procedure

may assign to the treatment group, say, those with high values of V and to the control group those with low V. In analy- zing results, the effect of the high Vvalues (i.e., B2V J) will be mixed with the treatment effect. An experimenter may rule out the possible effect of V by random assignment of subjects measured on V



Kinney 343

between groups. The sample subjects are measured on V, matched into pairs according to their V values, and one from each pair is randomly assigned to treatment. Thus, even for small samples the two groups will be approximately equivalent on V.

The passive observer has no opportunity to randomly assign sample subjects to treatment. Even experimenters may have dif- ficulty developing a satisfactory randomized design due to having too many potentially important Vs and Zs that must be simultaneously matched. Thus, in general, researchers face the problem of treatment groups that are not equivalent with respect to V.

For nonequivalent groups, there are three basic ways in which the researcher can mitigate the possible effects of the V factor in the model of equation 1. These are:

1. ignoring V(i.e., assuming or hoping that Vis randomized with respect to X),

2. matching on Vex post (i.e., matching after X has been chosen by the subject or assigned by Nature), and

3. using covariance analysis to statistically estimate and remove the effect of V.

The first approach ignores V, and results can be analyzed with a single-factor analysis of variance (ANOVA). The second approach physically equates the treatment groups with respect to V, and results can be analyzed using a randomized block design. The third approach "statistically" equates the groups, and results can be analyzed using analysis of covariance (ANCOVA).

Each of these approaches is discussed in turn, along with some of the advantages and limitations of each for experimenters and passive observers.

Ignoring V

As discussed above, ignoring a potential V is generally inadvisable due to the unknown effect of V. A negligible effect is the hopedfor result for any unmatched, unmeasured, or unknown Vs or Zs. How- ever, most real-world events have multiple causes and a negligible overall effect is unlikely. Furthermore, larger samples will not help in research designs that ignore systematic effects of V.

While expost matching and covariance analysis can't account for all possible Vs and Zs, they can reduce the risk that some potentially important Vs and Zs disguise the true effect of X. Figure 1 shows the relevant sampling distributions for the three approaches applied to the example. As shown in the relatively flat distributions on the left margin, ANOVA is based on the marginal distribution of Y with no consideration of V.

Ex Post Matching

In many situations, the researcher selects a sample after the phenomenon of interest has taken place. Often, the researcher selects a sample of subjects from the treatment group and then selects a subject from the control group with V equal or similar to V for each treatment subject. This ex post matching on V is probably the most commonly used design for passive observational studies in accounting.

For ex post matching, the model assumed to determine Y is:

m Y, = Bo +BIX,+ E BjMj +eij, (2)

j2

where Bo is the overall mean of Yplus the effect of (arbitrarily designated) match 1, Bj (for j> 1) is the differential effect of match compared to match 1, Mj is an indicator variable (equal to one if the sample subject is a member of match j and




zero otherwise), and m is the number of matches. '

For passive observational studies, it is impossible to randomly assign subjects to treatments since by definition the subjects have already either "self-selected" into treatment groups, or have been so selected by Nature. It is possible that there will be few or even no matches. For example, all the firms using straight-line depreciation may be small firms and all firms using accelerated depreciation may be large. A firm's choice of accounting method (or decision to change methods) may merely reflect its V value. Figure 1 illustrates such a possibility in that only the bottom half of group 1 can be matched with a member of group 0 due to the difference in V for the groups.

Even experimenters using ex ante matching with random assignment of subjects often face the lack-of-matches problem for at least some Vs and Zs. Sup- pose, for example, that a researcher believes that an auditor's response in a professional task experiment may be related to the auditor's professional training (X) after accounting for his or her mathematical abilities ( V). It may be difficult to match subjects from different firms based on mathematical abilities. This is because firms may hire and thus train (or students may choose firms and be trained) on the basis of mathematical ability.8

As will be discussed below, the efficiency of matching may be less than that for covariance analysis. However, expost matching is likely to be superior to covariance analysis when the functional form of the YlI V relationship is nonlinear or unknown. Given that the treatment effect is not cor- related with V, matching can be used for any functional form of Y and V (known or not) and analyzed using a blocked design.

Covariance Analysis

A researcher using analysis of covari-

ance (ANCOVA) statistically estimates the effect of V on Y and removes it. ANCOVA can be viewed as the result of projecting observed Y values along the regression line to a common point on the V axis, such as V, to yield the conditional distributions as shown in Fig- ure 1.1

Figure 1 shows that part of the difference between the marginal distributions of Yo and Y1 (as estimated using ANOVA) is due to a larger Vfor the treatment group. Matching (equation 2) accounts for the

difference by subtracting B O+ 1 BjMj from Y for each subject, and ANCOVA accounts for the difference by subtracting B0 + B2 Vij from Y for each subject. Thus, both matching and ANCOVA are seen to mitigate the differential effect of V. Fig- ure 1 also shows that control group subjects with relatively high Vfor the control group are matched to subjects with relatively low Vfor the treatment group. For matched designs, all other potential sample subjects must be omitted due to lack of matches.

Matching and ANCOVA yield more efficient (more precise) estimates of the treatment effect than does ANOVA. In general, however, it is unclear which of the two will be more precise. This is due to the fact that while the difference in Vo and V, reduces the precision of ANCOVA, the reduction in sample size due to lack of matches reduces precision for matching.

' The matches may be by individual subject ("precision" or "caliper" matching) as discussed above, or by frequency distribution (e.g., equal mean and variance with respect to V for both groups). A test of equality on V is often used as a justification for ignoring V in the statistical analysis.

I An alternative design is to limit all subjects in an experiment to a fixed level of V. This equalizes the effect of V but greatly reduces the generalizability of results over the range of reasonable V values that might occur.

I The sampling distributions for matching and ANCOVA are shown as the same in Figure 1 since the expectations of estimates of the treatment effects are the same for both. As discussed, however, their standard errors will differ.



Kinney 345

It is often difficult to predict which will be the greater problem. 10

Equation 1 and Figure I present a very simple situation even for a single V. For example, the YI Vrelationship may differ depending on whether X is at level zero or one. Furthermore, the occurrence of a given level of Vat time t-1 may have a direct effect on Y at time t but may also affect the level of X at time t which, in turn, affects Y at t. Thus, there may be two paths by which V affects Y. A com- plete approach would include a model of the "selection" process by which V affects X as well as the direct effects of X and V on Y."1

III. ALPHA, BETA, SAMPLE SIZE AND RESEARCH DESIGN

Planning research to disentangle X, Vs, and Zs involves four related factors. These are alpha (ce), beta (@), sample size, and what will be called the "research design" factor (denoted D). In a given situation, setting any three of them sets the fourth. The statistical factors of a (the probability of a type I error or incorrectly rejecting a true null hypothesis of no treatment effect), f3 (the probability of a type II error or not rejecting the null hypothesis when, in fact, there is a treatment effect), and sample size are well known. The research design factor is the ratio of two subfactors. Its numerator is the hypothesized magnitude of the (X) treatment effect (denoted 6), and its denominator is the standard deviation of the residuals in the equation used to estimate B1 (denoted a). Thus, D = 6/a. The numerator depends on the researcher's theory, and the denominator depends on how the researcher disentangles the Vs and Zs and the inherent variability in the phenomenon under examination.

The required sample size is a decreasing function of a, 3, 6 and an increasing function of a. Therefore, for a given a and 3, the required sample size will be small if

the proposed theory implies a large effect on Yand/or the researcher is clever in de- signing a plan to disentangle the effects of the Vs and Zs. For example, using ANOVA (no matching) in a single test with target ac=.05, 03=.1, and D=6/a=.5, the required sample size is 70 for each of the two groups. If the researcher has a theory yielding a larger 6 that would increase D to .75, then the sample would be 32 each, and if D is 1.0 then the sample size is 18 per group. Alternatively, for D=.5 and holding 6 constant, if matching is used and the Y., Y, correlation is .25 then the required sample is approximately 57 pairs."3 If the Yo, Y1 correlation is .5 (implying a reduction in aof about 18 percent), then the required sample is 36 pairs.

The four factors and their implications for accounting research will be discussed through two subtopics. These are: 1) power, and 2) prejudice against the null hypothesis.

Power

Consider a researcher who has a theory that the treatment effect (B1) is positive, and who therefore is interested in testing the (null) hypothesis that the true effect of treatment is less than or equal to zero against the alternative that the true effect

'0 ANCOVA will usually be less biased, however (see Cook and Campbell [1979, pp. 177-182], and Cochran [1983, pp. 127-128]).

" See Cochran's comments on R. A. Fisher's advice to "Make your theories elaborate. " According to Cochran, Fisher meant that when "constructing a causal hypothesis one should envisage as many different consequences of its truth as possible, and plan observational studies to discover whether each of these consequences is found to hold" [Rosenbaum, 1984, p. 43]. This advice is consistent with Boulding's exhortation to develop and test theories that are at the level of the real world.

12 The required sample size is:

n =2[(t., 2X-2 + 6, 2,-2 ) (1 /D)] 2

See Ostle [1963, p. 553] for a table. '" The required sample size is:

n = (1963,p + to55]) (f aD)]b'

See Ostle [ 196 3, p. 5 5 1] for a table.




is greater than zero. Assume that a sample of treatment subjects has been matched or "paired" on V with control subjects. Also, based on an assessment of the ap- propriate significance level for the issue at hand, the researcher has set a at .05, and the researcher has a research design in mind.

What the researcher may not consider at the planning stage is the magnitude of the hypothesized effect (i.e., a particular 6 for the alternative hypothesis) and the allowable 3 for that 6. 14 A 6 may not be considered since most theories suggest only the direction of an effect and not its magnitude, and f3 is not considered because no particular 6 is specified. The researcher may proceed to testing with little consideration of whether the planned test has an adequate chance to reject the null hypothesis even if it is false.

To illustrate, consider the sampling distributions in Figure 2. For both panels of Figure 2, the left-hand distribution is for the mean of the paired differences if the null hypothesis (B1 =0) is true, and the right-hand distribution applies if the particular alternative (B1 = 6) is true. Also for both panels, k is the point that yields a =.05 or five percent of the area to the right of the point under the left-hand distribution (i.e., Ho). In panel a, the research design and sample size yield a sampling distribution with a large area (1 - 3) to the right of k under the alternative hypothesis. Thus, there is high probability of rejecting Ho when the alternative hypothesis is true. In other words, the power of the test (1 - f) is high.

In Figure 2, panel b, 6 is the same as in panel a, but the sampling distributions are much flatter due either to small sample sizes or a large standard deviation due to remaining effects of Vs and Zs. Rather than the relatively high power test of panel a, the researcher faces a low power test. At a(=.05, 13 for the simple alterna-

tive hypothesis is greater than .5, and power is less than .5. Even if Ho is false (i.e., B = 6). and thus the researcher's theory of a positive treatment effect is correct, the researcher has a less than even chance of rejecting it!

Suppose that the researcher in panel b observes a test statistic that is almost significant, and the sample estimate of the treatment effect is equal to 5. He or she then decides to take a follow-up sample. The follow-up sample is also likely to in- dicate nonrejection due to its small size [Tversky and Kahneman, 1971, p. 107].

The real culprit, of course, is the low power of the test. If the low power is anti- cipated at the planning stage, an attempt can be made to mitigate its negative effects or else abort the project. In general, power can be increased by 1) increasing the sample size, or 2) increasing the design factor D by developing better theories (yielding larger 6) or by making better use of agiven sample size and theory by careful attention to the Vs and Zs (yielding smaller a).

As a practical matter, improved design is often the only alternative in accounting research since the size of samples in accounting frequently is effectively fixed. For experiments, the pool of available auditors, accountants, financial statement users, and even students is effectively lim- ited to fairly small numbers. Subjects' time is not free, and the supply is not inexhaust- ible. For passive observation, the number of firms for which particular accounting and other required economic data are available may be relatively small. Thus, accounting researchers need to be aware of a variety of analytical techniques appli-

4 See Tversky and Kahneman [19711. This is in contrast to classical or normal distribution theory-based audit sampling where, in addition to setting a to control the risk of incorrect rejection, the auditor sets i to control the risk of incorrect acceptance and sets 6 based on "intolerable" error (materiality). The auditor then selects an estimator and calculates the minimum sample size subject to the target a, j, and 6.



Kinney 347

FIGuRE 2

SAMPLING DIsRIuBUTIONS OF d * FOR HIGH AND Low POWER TESTS

a. High Power I I

OI _ _ _ _ _

Reject ~ Reec Ho

b. LowPower Rt

l~~~~~~~~~~~ l.0 l l~~~~~~~~

I

l~~~~~~~~~~~~~Rc Ho lY~ l o)M jlal

cable to a variety of research problems. 15 Furthermore, for a given research par-

adigm, the problem of low power is likely to become more difficult over time. Other things equal, as knowledge of the effects of accounting expands, the likely size of the effect of each new or more refined theory (B1) will tend to have less addition- al explanatory power. As knowledge expands, the best potential Xs are investi- gated and become Vs or Zs. For example, early studies tested hypotheses about the

degree of owner versus manager control as an X that affected accounting choices. Later studies have used the same variable as a Vor Z. Absent developments that re- structure the way a particular problem is addressed, future researchers will be faced with discovering new Xs that have less potential explanatory power.

's In debate on the preferability of parametric vs. non- parametric statistics in research, the ability of parametric methods to accommodate more Vs and Zs through covariance analysis is an often overlooked advantage.




In fact, it may be unreasonable to expect that a particular theory based on accounting methods will yield a true differential effect that is very large relative to the variance of Y. How things are accounted for simply can't be expected to explain a large portion of stock price variability or managerial or investor behavior. Under some conditions, the sample size required to yield reasonable power exceeds the size of the known population!

A researcher can get some protection by making a tentative calculation of power before investing in expensive data collec- tion or in experimentation. For example, passive observers of accounting changes and stock returns may be able to make reasonable estimates of the standard deviation of return residuals and might make power estimates for various levels of 6. 16

If the estimated power is inadequate even for the maximum 6 that might reasonably exist, then the research can be redesigned or aborted. Experimenters are perhaps more familiar with prospective power cal- culations and frequently use a pilot sample to assist with the sample size and research design development.

Prejudice Against the Null Hypothesis

A theory usually specifies the direction of the treatment effect and a researcher generally sets out to reject hypotheses based on the assumption that the treatment effect is zero or in the opposite direction from what the theory predicts. The focus on rejecting the null hypothesis is the source of a number of "biases" against the null that may lead to dysfunctional consequences. Greenwald [1975] lists eight such consequences; four that seem most important for accounting researchers are discussed in order to be better able to avoid them.

1. A paper will not be submitted for publication consideration unless the

results against the null are "significant." Especially interesting or in- novative results may be submitted on higher than .05 significance (or alternatively, the probability at which the results are significant are reported), but rarely does an editor see results with significance levels above .15. This prejudice need not exist if not rejecting the null gives reasonable credibility to the null."7

2. Ancillary hypotheses will be ele- vated in the exposition of results. Secondary hypotheses that are significant ex post will receive more attention than other secondary hypotheses and perhaps the primary hypotheses. Suggestions will be made that these results warrant further study, when in fact one would expect about one in ten non- sense relationships to be significant at the .10 level.

3. Alternative operationalization of variables or their functional form will be conducted only if "prelimi- nary" results are insignificant. The extent to which this search activity is justified is open to debate since most theories don't imply a single measurement or functional form.

4. The search for errors will be asym- metric. Outliers that impede rejection of the null hypothesis will tend to receive more diligent attention than those that favor rejecting the null. If significant results are

16 The choice of 6 is somewhat arbitrary, but in planning it is useful to consider reasonable or plausible values for the true treatment effect of X. Alternatively, one might choose the smallest effect that informed persons would agree is empirically "important" and therefore worth knowing about if it exists, or the largest amount that one could reasonably expect.

" In classical statistics, not rejecting the null is not equivalent to accepting the null. However, non-rejection by a reasonably powerful test or series of tests does increase one's subjective degree of belief in the null.



Kinney 349

obtained on the first analysis of a problem, the neophyte researcher may not consider a search for outliers or for other violations of statistical assumptions underlying the analysis. Nonrejection may lead one to consider such explanations and to search for programming errors and data coding errors.

V. SUMMARY AND CONCLUSIONS

In this paper we have stressed consideration of planning for Vs and Zs to be able to isolate the effect of X as a potential explanation of differences in Y. This consideration may allow increased power in tests and may allow more to be learned from a given sample. Planning for Vs and Zs can reduce the risk of not rejecting the null hypothesis when it is false. Such planning may also allow a basis to argue that nonrejection of the null hypothesis may support acceptance of the null. That is, if the treatment has an important effect, then it should be revealed by the test. Thus, some- thing may be learned whether results are statistically significant or not. This should increase the objectivity of the researcher, since the work is valuable whatever the empirical results.

There are at least two ways in which the approach discussed in this paper can be useful to Ph.D. students. One is in evaluating the research design of others, and the other is in planning the student's dissertation. 18 Students must evaluate the work of others whether in published articles, working papers, or accounting research workshops. A student applying the approach to the work of others might try to answer the following questions: What is the Y and what is the X? What Vs and Zs

are considered? Are there better ways to account for the effects of Vs and Zs? What are other Vs and Zs that might have important effects?

The same approach can be applied by the student to his or her own dissertation proposal. While the basic development of a research proposal is the responsibility of the student, there is much to warrant early faculty discussion of planned dissertation research. That is, the faculty can evaluate a proposal by considering the reasonable- ness of the theory and the adequacy of control of potential Vs and Zs. The faculty should be asked: Is the magnitude of the hypothesized effect plausible? Are all important competing explanations listed and adequately dealt with in the plan? Will the proposed tests likely uncover evi- dence of a difference equal to 6 if it exists? Will nonrejection lend credibility to the null?

Faculty approval of planned dissertation research reduces the student's risk by 1) ruling out potential topics that have little chance of successful completion, 2) gathering the right data on the first attempt, 3) eliminating outcome dependence (thus reducing moral hazard for the student), and 4) reducing the temptation of the student (and faculty) to pursue num- erous tangents that may come to light as the research progresses.

1 In planning research or evaluating the research of others, a useful practice is to give early attention to the purpose of the research through preparation of a three- short-paragraph abstract, synopsis, or working model of the research. The first paragraph answers the question "What is the problem?" The second asks, "Why is it an important problem?" and the third, "How will it be solved?" Alternatively, the questions might be: "What are you (or the researcher) trying to find out?", "Why?", and "How will it be done?"




REFERENCES Abdel-khalik, A. R. and B. B. Ajinkya, Empirical Research in Accounting: A Methodological Viewpoint,

Accounting Education Series No. 4 (American Accounting Association, 1979). Ashton, R. H., Human Information Processing in Accounting, Accounting Research Study, No. 17

(American Accounting Association, 1982). Ball, R. and G. Foster, "Corporate Financial Reporting: A Methodological Review of Financial

Research," Studies in Current Research Methodologies in Accounting: A Critical Evaluation," Journal of Accounting Research (Supplement 1982), pp. 161-234.

Boulding, K. E., "General Systems Theory-The Skeleton of Science," Management Science (April 1956), pp. 197-208.

Cochran, W. G., Planning and Analysis of Observational Studies, edited by L. E. Moses and F. Mosteller (John Wiley & Sons, Inc. 1983).

Cook, T. D. and D. T. Campbell, Quasi-Experimentation Design & Analysis Issues for Field Settings (Houghton-Mifflin Company, 1979) especially chapters 3 and 4.

Greenwald, A. G., "Consequences of Prejudice Against the Null Hypothesis," Psychological Bulletin (January 1975), pp. 1-20.

Lev, B. and J. A. Ohlson, "Market-Based Empirical Research in Accounting: A Review, Interpretation, and Extension," "Studies in Current Research Methodologies in Accounting: A Critical Evaluation," Journal of Accounting Research (Supplement 1982), pp. 249-322.

Libby, R., Accounting and Human Inlormation Processing: Theory and Applications (Prentice-Hall, Inc., 1981).

Ostle, B., Statistics in Research, 2nd Edition (The Iowa State University Press, 1963). Rosenbaum, P. R., "From Association to Causation in Observational Studies: The Role of Tests of

Strongly Ignorable Treatment Assignment," Journal of the American Statistical Association (March 1984), pp. 41-48.

Simon, J. L., Basic Research Methods in Social Science: The Art of Empirical Investigation, 2nd Edition (Random House, Inc., 1978) especially chapters 3, 7, and 11.

Tversky, A. and D. Kahneman, "Belief in the Law of Small Numbers," Psychological Bulletin (August 1971), pp. 105-1 10.

Watts, R. L. and J. L. Zimmerman, Positive Accounting Theory (Prentice-Hall, 1986).



empirical accounting research design for ph.d. students

Documents