Since June 1, 2008, I’ve had the honor and privilege of serving as an editor of The Accounting Review. In this role, I get to see a lot of papers in the financial-archival area, although there are four other editors plus senior editor Steve Kachelmeier also looking at papers in this area, so I don’t get to see them all. Nevertheless, after looking at 40 plus papers over the last year, I’ve started to notice some patterns. One of these patterns is the topic of this post: the relation between research contribution and editorial outcome. Disclaimer: these are my thoughts based on my own observations, and I don’t speak for TAR or any of its other editors.

A surprisingly high percentage of the papers assigned to me that fail to survive the first review round are rejected due to contribution issues. In many cases, these papers are well-written reports on carefully conducted, well-designed research with no identifiable technical defect, but get rejected anyway due to absence of contribution. Also surprisingly, some of these are papers drawn from the authors’ dissertations, suggesting that dissertation advisers may not have been able to identify the potential absence of contribution before their students committed to the dissertation topic. I feel terrible every time I need to write a letter rejecting one of these papers (after being advised to do so by reviewers) since smart, capable people have spent enormous amounts of time on them. It has occurred to me that not everyone has the same thing in mind when referring to contribution, so I would like to talk about what I mean by contribution and give some examples of research where contribution is likely to be an issue.

In 1964, Justice Potter Stewart tried to explain pornography, or what is obscene, by saying, “I shall not today attempt further to define the kinds of material I understand to be embraced . . . but I know it when I see it . . . ” The same might be said about accounting research contribution; it is difficult to define but might be most easily understood by looking at a few examples. Before continuing, think about each of the following hypothetical research results. Try to decide if each is likely to pass muster as making a contribution to accounting research:

  1. A study finds that firms are more likely to manage earnings after institutional owners make large block share purchases.
  2. Post-earnings-announcement drift is documented to occur in Singapore and Hong Kong.
  3. Applying a new methodology, research shows that stock prices are not related to individual investors’ potential dividend taxes on corporate retained earnings. One prior study shows this same result and one prior study shows the opposite result.
  4. A paper documents the accrual anomaly for the first time for financial firms.


  1. Documenting that a previously identified relationship is conditioned on or depends on a new variable can make a contribution. For example, if prior research documents that opportunistic accounting (earnings management) occurs when managers have incentive X, documenting that earnings management is less likely in the presence of incentive X when the firm has control Y in place would be a useful contribution (e.g., X=earnings below analysts’ consensus and Y=higher proportion of independent board members). However, at the current point in the evolution of this research area, identifying a new incentive X and showing that it is related to earnings management is not likely by itself to be a contribution. We have plenty of research showing that managers behave opportunistically when given the chance, and we are unlikely to learn much from an additional study with that same finding, so I would say hypothetical A above is likely to be rejected due to lack of contribution. In my view, however, research that helps us understand how opportunistic accounting is related to cross-sectional differences in firm characteristics or compensation arrangements is still potentially useful.
  2. Another example relates to international research. Replication using non-US data of a published study based on US data is a research strategy likely to lead to questions about contribution. For example, a study showing that post-earnings-announcement-drift exists in Singapore and Hong Kong as well as the US is not useful by itself and would likely be rejected. However, a study that identifies differences in accounting standards (e.g., differences that affect asymmetric timeliness of earnings) or in institutions across countries and relates these differences to predictable differences in drift would be much more interesting. The results of such a study could tell us about the relation between drift and the particular accounting standards or institution studied, which is more important than simply confirming the cross-border existence of drift.
  3. Research that resolves conflicting evidence is potentially useful, especially if it allows us to understand why the conflict arose in the first place. That is, suppose we have published papers finding X when using method Y and finding X’ when using method Z, and a new study finds X when using method W. This new result is least useful if it is viewed as simply another item on a scale pointing toward X rather than X’. The result is most useful if something can also be said about why methods Y and W are credible but method Z is not (e.g. methods Y and W have some feature that is missing from method Z).
  4. A common error is to equate novelty and contribution. For example, a paper might say “To our knowledge, our study is the first to examine the accrual anomaly in financial firms.” This might be a useful study, but not because it is new. Specifically, the study could be useful if there is a difference X between financial firms and non-financial firms that is a candidate for explaining the accrual anomaly, and if looking at financial firms could provide evidence that the accrual anomaly is or is not related to X.

Other thoughts:

One idea I see expressed frequently is that research makes a contribution if regulators, financial statement users or financial statement preparers can learn something with practical implications from the research. Accordingly, many papers make unsupported claims for the benefits of their findings for these audiences. I think this standard for contribution sets the bar too high. Even a study that is of interest only to academics can make a contribution if it provides new evidence with the potential to reject existing theory or to help us understand documented empirical relationships. So there is no need to overclaim for usefulness to non-academic audiences, especially if the overclaiming is not convincing.

A piece of advice I might offer is to try to identify the potential contribution of the research before starting to work on a project. All too often, researchers begin by collecting sample data, running regressions and constructing tables. Then they sit down to write the “front end” of the paper. Sometimes, the introduction is the last component of the paper to receive attention. It is preferable to write the introduction first, before beginning empirical analysis (it can and almost certainly will be revised later). Be sure to include a paragraph in the introduction that begins with “The contribution of this study is…” or similar language. After you have a draft of the introduction, show it to colleagues and collect feedback before proceeding. If you find that people don’t buy the contribution of the study, don’t proceed until you refine your vision of the study to the point where others can clearly see the contribution. It’s much better to resolve this issue up front rather than to hear about it from reviewers and editors after a year of elapsed time and hundreds of hours of work. I also suggest that dissertation advisers get their students started this way when working on finding dissertation topics.