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DISCUSSION OF: Subordinates as the First Line of Defense against Biased Financial Reporting

2012; American Accounting Association; Volume: 24; Issue: 1 Linguagem: Inglês

10.2308/jmar-50213

1558-8033

Kristy L. Towry,

Auction Theory and Applications

I appreciate the invitation to comment on this paper by S. Jane Jollineau, Tom Vance, and Alan Webb (Jollineau et al. 2012). It is an interesting piece of research, and reading it brought several (somewhat disparate) issues to mind. These issues include the role of intuitive theory in experimental research, the limits of experimental research for examining effect sizes, and the values that our community holds with regard to deception in experimentation. In choosing these particular issues, I will admit to being somewhat opportunistic in that I have chosen issues about which I have strong opinions. Thus, I will use this paper as a jumping-off point, and freely stray away from the details of this paper and toward these larger issues. Whereas most of my attention will be dedicated to addressing these issues, I will arrive at them in due course, following a standard outline of review. That is, I will first summarize the primary strengths of the paper, and then move on to summarize my interpretations, concerns, and thoughts (both with regard to theory and predictions and experimental methods). Finally, I will discuss briefly some potential extensions.This paper has a number of significant strengths. I will limit my comments to two that I see as particularly notable. First, I believe it is important to move beyond our simple two-layer model of the firm as derived from traditional agency theory. The canonical principal-agent model is elegant in its simplicity, and it is applicable for studying employment contracting in a wide variety of contexts. That is, part of the traditional agency model's power lies in its departures from reality, because these departures allow us to abstract away from the contextual details and to make broad observations about the underlying economic forces at play. However, it is important to identify situations in which the two-layer model is limited in its applicability, and I believe that the authors of this paper have identified one such area. The idea that they examine—that a subordinate may act as a controlling mechanism over the behavior of a manager, who acts in his or her own interest rather than in the owner's interest—is intriguing, and offers the potential for a worthwhile expansion of the literature, both theoretical and empirical. And the paper's interesting and important revelation is that something we would normally consider almost universally positive (high-quality relationships across hierarchies of the organization) can have a negative impact on the organization from a control perspective.Another strength of the paper is that the story rings true. My own intuition, based on my reading of the literature, as well as real-world experience, tells me that subordinates can indeed serve as an important first line of defense against managerial opportunism. This same intuition further suggests that the quality of the relationship between superiors and subordinates can affect deeply how well that control works. Some might read this comment and assume that the JMAR copyeditors have missed a typographical error. Surely, a discussant is not suggesting that an intuitive theory is a strength, rather than a weakness, of a paper. But this is exactly what I am suggesting. One of the most common critiques we see in referee reports is that the theory is “too intuitive” or that the results are not surprising. I would like to argue here that this is a bad comment.Our theories should be intuitive. That is, before we construct an empirical test of a theory, we should scrutinize the theory from the perspective of face validity. Unfortunately, we often treat the face validity check as a substitute for empirical evidence. As reviewers, we are quick to say that there is little contribution in testing a theory that passes the face validity check, and this is bad for the progress of our field. To be clear, I am not suggesting that we need to reexamine ad nauseam theories that have been validated through prior empirical research. There is no need to test things that we already know to be true. But there is great value in testing the validity of theories we simply believe to be true because they are intuitive. If we reject as unimportant tests of intuitive theories, we face two important risks. The first risk is that we will simply go on believing to be true something that is, in fact, false. The second risk is that we will encourage poorly developed, convoluted theories, as authors embark on a “search for surprise.” The very idea that a field of scholarly enquiry would progress by looking for non-intuitive, surprising results is absurd at best and dangerous at worst. In fact, I would argue that it is the academic equivalent of sensationalistic journalism, appealing to a desire for entertainment rather than a scholarly quest for knowledge.Imagine a patient who visits the physician's office to describe a number of symptoms. The doctor listens to the patient's descriptions and concludes that the patient likely is suffering from a mild condition, and that the symptoms will likely disappear on their own within a few weeks. This is the doctor's theory, and it is quite intuitive. However, there is a remote chance that the symptoms are caused by a much more serious condition—one that will require quick intervention to prevent further deterioration. Imagine, now, that the doctor offers to perform a simple blood test to help determine which condition is causing the symptoms. The results of that test would probably be unsurprising. They would likely confirm what the doctor already believes to be true—that the patient is not seriously ill. However, if I were this patient, I would find great value in the test. If physicians applied the norms of accounting researchers, they would likely neglect such tests, because it's not so interesting to confirm one's intuition. (Admittedly, the analogy is not perfect—a mistake in the medical field could be deadly, whereas I am unaware of anybody suffering fatal consequences from believing the wrong accounting theory.)Other researchers (e.g., Maines et al. 2006) have argued that impactful research is that which leads to legitimate, consequential belief revision. How can one reconcile my advice to test intuitive theories with this often-cited criterion? These ideas are not as far apart as one might suspect. We can conceptualize our understanding of various phenomena of interest as a collection of probability distributions, which can be described partially using the attributes of means and variances. The mean of any given distribution represents a theory—our belief about how the world works. The variance represents our level of certainty regarding the theory's validity. I argue here that there is value in research that revises either of these distributional attributes. Research that causes a mean shift—a change in what we believe to be true—is impactful and can change the direction of the literature. However, research that reduces the variance around those beliefs is also crucial as a field matures. One study rarely provides clear, irrefutable evidence on any particular phenomenon, so even a published paper likely leaves some variance in our distribution of beliefs. Therefore, replications can provide value in further reducing that variance. If we value only that research which shifts the means of belief distributions, we risk building a body of research that is shallow and fragmented. If we neglect the research which reduces the variances of our belief distributions, then our field will progress as a series of assumptions layered upon assumptions.H1 predicts a directional main effect of relationship quality on bias in accounting estimates. Specifically, it applies leader-member-exchange (LMX) theory to predict that as the quality of the relationship between superior and subordinate increases, subordinates will become more willing to comply with their superiors' requests for biased estimates. H2 extends this argument, suggesting that the degree to which the subordinate perceives the accounting estimate task to be ethical in nature will predict the degree to which she or he will comply with the superior's request for a biased estimate. While the paper describes this prediction in terms of bounded ethicality, one might alternatively consider it from the perspective of framing. We know that when decision makers frame a decision as an ethical dilemma, it fundamentally changes the factors that they consider in making the decision (Tenbrunsel and Messick 1999). These hypotheses, pictured in Figure 1, are logical and are supported. While H1 and H2 predict two main effects, I might have expected to see an interaction such that subordinates who do not frame the decision as an ethical dilemma would readily comply with the superior's request, regardless of relationship quality. I wonder why the authors did not explore that possibility.H3, pictured in combination with H1 and H2 in Figure 2, adds another independent variable, the direction of the superior's request. The prediction is that the effect of the subordinate's beliefs about the ethics of the situation (predicted in H2) will be greater when the request from the superior is for an income-increasing estimate than when it is for an income-decreasing estimate. This is an interesting and subtle argument, hinging on the notion of accounting conservatism. The argument is that due to the principle of accounting conservatism, an income-decreasing estimate is likely to be viewed as less unethical than is an income-increasing estimate. Therefore, the subordinate's beliefs regarding the ethicality of the estimation task do not play as large a role for income-decreasing requests from the superior.H4 predicts another two-way interaction. This prediction, pictured along with the prior three hypotheses in Figure 3, is that the effect of relationship quality (as predicted in H1) will be greater for income-decreasing requests than for income-increasing requests. This is the hypothesis with which I have struggled the most. The argument is that when the effect of ethicality judgment is small, as in the income-decreasing condition (H3), the effect of relationship quality will be allowed to dominate. This reasoning is based on an underlying assumption that the total effect size (the aggregate of the effects of relationship quality and ethicality judgment) is in some way bounded, such that when the effect of the ethicality judgment decreases, the effect of relationship quality can increase more readily. I can think of no theoretical basis for such a substitution effect. The total effect size may be bounded in the laboratory, due to artificial constraints in the experimental setting. However, it is unclear why it would be bounded in the real world, and so I question whether the theory being proposed here generalizes outside of the laboratory.I see the issue with the H4 prediction as related to a larger issue, and that is the limitations that experiments face in terms of teaching us about effect sizes. Experiments are good at testing theories (i.e., testing the direction of a specific, isolated effect). As such, they are the gold standard of methods for assessing causality. They are not, however, good at testing effect sizes. The experimental setting is by definition artificial, and effect sizes can be arbitrarily affected by parameterization choices. So, experimentalists should practice caution in making generalizations regarding the size of effects, in comparing the sizes of various effects within one laboratory experiment, and in assessing the aggregate effect of multiple effects. If I understand the reasoning correctly, the prediction made through H4 in this study is essentially one of effect sizes and, therefore, not of the form that is best examined in an experimental setting.There are several experimental design choices in this study worthy of comment. First, I was initially bothered by the design choice that prevented the superior in the study from detecting whether the subordinate had complied with the request. However, the authors have done a nice job of explaining that this lack of mundane realism is a strength of their study, in that it allows them to isolate more effectively the effects in which they are interested.Second, the study uses a within-subjects manipulation of the requested bias direction, which naturally brings to mind concern for demand effects. However, the authors have made a convincing argument that given the complexity of their design, including interaction effects in addition to main effects, it is unlikely that demand artifacts are responsible for the results.Finally, the authors of this study have gone to great lengths to avoid the use of deception in their experimental design. I understand the reasoning for this choice, because a large contingent of the experimental accounting community is strictly against the use of deception in any form. This view is consistent with that of the experimental economics community, and is based both on ethical and on practical considerations (i.e., concerns regarding subject pool contamination). Notably, however, another large group of accounting scholars is comfortable with the use of deception, and would argue that the use of innocuous deception in laboratory studies improves the quality of our research, allows us to study topics that would otherwise be impossible, and provides no harm to the participants. In fact, these scholars, whose thinking is more in line with that of experimental psychologists, would challenge the ethics of the sometimes convoluted design choices made by researchers avoiding the use of deception, on the grounds that these design choices result in unnecessarily wasted subject time. My observation is that for some scholars, their opinions on this topic are almost religious, rather than being based on reason. Our young scholars can easily become victims of a holy war when they are faced with reviewers from different religious sects. I will not resolve this complicated debate in this short discussion. However, I will argue that it is important for our community to continue to discuss the use of deception, with the goal of developing shared values. (For discussions of the merits and costs of deception, see, e.g., Bonetti [1998] and Ortmann and Hertwig [2002].)I appreciate the invitation to discuss this paper and the opportunity to pontificate on a few issues that I see as important to our research community. In summary, I argue in this commentary on three primary topics. First, I argue for the importance of testing intuitive theories, suggesting that there are great costs to instead creating a research program by “searching for surprise.” Second, I caution against using experiments to test and make conclusions regarding effect sizes. Finally, I press for a continued conversation regarding the use of deception in experiments, with the goal of achieving shared values.In addition to these general topics, I would like to conclude by thinking about how the questions addressed in this study might be extended as the literature moves forward. As mentioned earlier, a compelling take-away from the study is that positive relationships between levels in the organizational hierarchy might have a negative consequence. That is, they may lead to greater compliance with superior requests for bias in accounting estimates and other financial reporting. This result may be interpreted as somewhat troubling, but the authors provide us some hope in the form of mitigating forces. The fact that ethical beliefs can mitigate compliance with requests for biased estimates implies that increasing awareness or salience of the ethical nature of the estimation task might yield benefits. Future research might explore other potential mitigating factors. For example, could strong ties to the accounting profession serve to mitigate the pressure to comply with requests for bias? Prior work on professional affiliation among auditors may provide some guidance on this topic (e.g., King 2002). I look forward to watching this literature progress and to learning more about how subordinates can serve as a first line of defense against biased financial reporting.