Opening Remarks

Topic Selection

I believe that the choice of research problem, choosing the phenomena we wish to explain or predict, is the most important decision we make as a researcher. We can learn research method. Albeit with greater difficulty, we can also learn theory-building skills. With some tutoring and experience, we can also learn to carve out large numbers of problems that we might research. Unfortunately, teasing out deep, substantive research problems is another matter. It remains a dark art. Weber (2003)

You have mapped different perspectives of the challenge, but not yet a topic: a topic is the specific, defensible claim about why this tension deserves a review. This session gives you the criteria to make and test that claim before you invest a semester in it.

Learning Outcomes

By the end of this unit, you will be able to:

Diagnose whether a topic candidate is shaped by a phenomenon or by a familiar method or theory, and correct course if it is the latter.
Test a topic candidate against five criteria, significance, novelty, curiosity, scope, and actionability, and name honestly where it is weakest.
State a topic as a defensible claim about why a tension deserves a review, in a domain-phenomenon-knowledge-problem structure that argues for its relevance to both academia and practice.

Effective Research Topics

Focus Areas

To find an effective topic you need to identify (Recker, 2021, p. 36)

a specific domain with an
important phenomenon that deserves attention from academia and that relates to a
problem with the existing knowledge about this type of phenomenon.

Criteria for Effective Topics

Colquitt & George (2011) put forth five distinct criteria for effective topics in information systems and management science: Significance, novelty, curiosity, scope, and actionability

Significance

Taking on “grand challenges”

Identify and confront or contribute to a grand challenge.¹
Tackle such problems in a particular area of inquiry (i.e., slicing the elephant).
Try to make a contribution that is useful in theory and that will benefit individuals and society.
Try a new approach that is different from the usual explanations.
Articulate clearly how the study solves a piece of a larger puzzle.

Example:

Ferlie et al. (2005) took on a grand challenge in asking why evidence-based innovations failed to spread in the health care industry.

They addressed why beneficial innovations fail to spread across organizations despite proven effectiveness.
They examined healthcare innovations in the UK NHS, specifically how professional groups mediate adoption decisions.
Their research extended innovation theory by highlighting professional mediation while providing practical insights for healthcare implementation strategies.
They shifted from traditional organizational or environmental factors to focus on professional identity, knowledge bases, and power dynamics as innovation filters.

Novelty

Changing the conversation

Consider if and how your review might change the conversation already taking place in a given literature.²
Aim at either adding momentum to a conversation or giving it a new direction.
Generate new and creative solutions by exploring new domains, rather than preferring the familiar, the mature, and perspectives near existing approaches, that is, avoid the familiarity, maturity, and nearness traps.

Example:

Agarwal et al. (2004) focused on a new, under-researched area by investigating how the knowledge capabilities of industry incumbents affected the generation, development, and performance of “spin-outs.”

They shifted knowledge transfer literature from focusing on alliances and partnerships to employee mobility and spin-outs as knowledge transfer vehicles.
They introduced the “knowledge inheritance” concept, connecting entrepreneurship with knowledge management in a novel way rather than just adding to existing approaches.
They studied an understudied phenomenon (spin-outs) instead of well-established mechanisms like licensing or joint ventures, using longitudinal survival analysis instead of typical cross-sectional methods.

Common Topic Traps

Familiarity and nearness trap: Picking a topic that is too familiar and/or too close to the existing literature, which may only offer contributions that are not sufficiently different from existing perspectives.
Maturity trap: Selecting a topic that is too mature, which may only offer redundant contributions.

Curiosity

Catching and holding attention

Topics are interesting when their propositions counter a reader’s taken-for-granted assumptions (e.g., showing a seemingly good phenomenon to be bad).
Try to identify and use surprising findings that cannot be explained by methodological issues or existing explanations, that is, “breakdowns” that signal the potential existence of a mystery, such as inconsistent findings.³
Try to reframe, reformulate, or solve the “mystery.”

Example:

Van Kleef et al. (2009) strived to solve the mystery of contradictory findings about the effects of leader displays of emotion. They studied whether team performance would be facilitated by leaders displaying happiness or by leaders displaying anger.

Scope

Casting a wider net

Even the best topic ideas can be undermined if the resulting study is too small.
Reviews cannot tackle grand challenges if they are not ambitious in scope.
Aim to fully and comprehensively sample the landscape in a given domain, that is, relevant constructs, mechanisms, and perspectives.
You may even include constructs and mechanisms derived by using multiple lenses.

Example:

Seibert et al. (2001) examine the effect of social capital on career success. They include all three theoretical perspectives on social capital that can explain why and how the characteristics of a personal social network can impact career success.

As a team producing a systematic review rather than a single primary study, you can sample a domain far more comprehensively than an individual master’s thesis, constrained to one person, one semester, one method, ever could. Treat scope as an ambition to raise.

Actionability

Offer insights for managerial or organizational practice

McGahan (2007) outlines five major ways that management studies can be actionable:

Offering counter-intuitive insights.
Highlighting the effect of new and important practices.
Showing inconsistencies in and consequences of practices.
Suggesting a specific theory to explain an interesting and current situation.
Identifying an iconic phenomenon that opens new areas of inquiry and practice.

Conclusion

An effective topic …

allows researchers to tackle a grand challenge in a literature,
pursues a novel direction,
maintains curiosity,
builds a study with ambitious scope, and
uncovers actionable insights.

Excursus: Team Agreement

Working Agreement

A good topic chosen by a team that cannot make decisions together will still fail.

Before you commit to a topic, settle how you will work as a team for the rest of the semester. A working agreement keeps a disagreement about the topic from turning into a disagreement about the team.

Agree explicitly on:

Roles. Who owns which part of the review protocol, the writing, the coordination with coaching? Roles can rotate, but someone should be accountable for each deliverable at any given time.
Decision rules. When you disagree about a screening judgement call or a framing choice, how is it resolved: majority vote, the person who did the reading decides, escalate to coaching? Decide this before you need it, not during the disagreement.
Meeting rhythm. A fixed weekly slot, even short, outperforms ad hoc meetings called only when something is urgent.

Write this down. A one-page working agreement, agreed once, saves far more time than it costs.

Homework

Draft your topic statement.

Using the three focus areas from the start of this session, write, as a team:

Your specific domain.
The important phenomenon within it.
The problem with existing knowledge about that phenomenon.

Then check it against all five criteria (significance, novelty, curiosity, scope, actionability) and name honestly where it is weakest.

Literature

Agarwal, R., Echambadi, R., Franco, A. M., & Sarkar, M. (2004). Knowledge transfer through inheritance: Spin-out generation, development, and survival. Academy of Management Journal, 47(4), 501–522.

Colquitt, J. A., & George, G. (2011). Publishing in AMJ—part 1: Topic choice. Academy of Management Journal, 54(3), 432–435.

Ferlie, E., Fitzgerald, L., Wood, M., & Hawkins, C. (2005). The nonspread of innovations: The mediating role of professionals. Academy of Management Journal, 48(1), 117–134.

McGahan, A. M. (2007). Academic research that matters to managers: On zebras, dogs, lemmings, hammers, and turnips. Academy of Management Journal, 50(4), 748–753.

Recker, J. (2021). Scientific research in information systems: A beginner’s guide (2nd ed.). Springer.

Seibert, S. E., Kraimer, M. L., & Liden, R. C. (2001). A social capital theory of career success. Academy of Management Journal, 44(2), 219–237.

Van Kleef, G. A., Homan, A. C., Beersma, B., Van Knippenberg, D., Van Knippenberg, B., & Damen, F. (2009). Searing sentiment or cold calculation? The effects of leader emotional displays on team performance depend on follower epistemic motivation. Academy of Management Journal, 52(3), 562–580.

Weber, R. (2003). Editor’s comments: The problem of the problem. MIS Quarterly, 27(1), iii–ix.

Footnotes

Grand challenges are large, important, unsolved problems, reflected for instance by the United Nations’ Millennium Development Goals to eradicate global poverty, disease, and hunger.↩︎
Adding to a conversation requires knowing the conversation. Research topics come from reading extensively in the literature.↩︎
According to Colquitt & George (2011), such topics arouse more interest than the more typical “gap-spotting” approach to generating research questions.↩︎