Effective Topics

Research Project 1 (RP1) — U4

Andy Weeger

Neu-Ulm University of Applied Sciences

September 1, 2026

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)

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

Exercise

Two of Weber (2003)’s three mindsets that keep researchers from confronting the problem of the problem are already settled for you: your map anchors you in a phenomenon, not a theory, and your method is fixed as a systematic literature review. What remains live is theory and authority.

Diagnose how you are narrowing your candidates.

1. Of your candidate phenomena, are you leaning toward the one with the strongest evidence in your map, or the one that is easiest to explain with a theory your team already knows?
2. Which practitioner’s claim carries the most weight in your current choice: the one with the clearest tension, or the one from the most senior, vocal, or familiar source?
3. Reread the tension you are leaning toward. Does it still read as the practitioners’ problem, or has it already drifted toward a problem only a researcher would recognize?

20:00

Weber (2003) names three mindsets that keep researchers from confronting the problem of the problem: an identity built on method rather than problem, a have-theory-will-travel habit of reapplying an existing theory instead of building one, and subservience, drifting toward whatever topic is comfortable for a supervisor (or industry partner).

Two of these are already decided for you. Your Map of Perspectives anchors your candidates in a phenomenon, not a theory. Your method for this semester is fixed too: every team runs a systematic literature review, to establish what is and is not yet known before semester 2 and 3 commit to primary research, regardless of which phenomenon it picks.

What remains live is theory and authority: which candidate you favor because it is easiest to explain with a framework your team already knows, and whose claim you favor because of who said it rather than how strong the tension is.

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, 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.

Discussion

What challenges are
you interested in?

In which area of inquiry could your project contribute to it?

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.

Discussion

What is required to
identify a novel topic?

What can you do to identify a topic that is not too mature and/or too close to existing literature?

• Look for emerging phenomena: study new technologies, business models, or social trends before they become mainstream research topics.
• Examine established concepts in new contexts: apply mature theories to novel settings.
• Focus on paradoxes and anomalies: investigate cases where established theories fail to explain observed phenomena.
• Look for “white spaces”: map existing literature to identify unexplored intersections between established research streams.
• Question assumptions: what’s taken for granted in your field that might not be?
• Study failures and negative cases: examine when established practices don’t work or expected outcomes don’t materialize.

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.

Discussion

What are “mysteries” you have identified in your industry inputs?

Go back to your U2 perspective notes for a genuine breakdown: a case where two practitioners described the same fact pattern but drew opposite conclusions from it, rather than a mere disagreement of opinion. Treat that contradiction, rather than the loudest opinion in the room, as the phenomenon worth investigating.

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.

Exercise

Each of the four problem sections discussed in Brown et al. (2026) closes with a “From Practitioner Problem to Research Opportunity” passage that converts one practitioner concern into two to four open, question-form research opportunities.

Apply the practitioner-to-research move.

1. State your identified industry tension the way the editorial states a practitioner problem: one paragraph, no research jargon.
2. Write two research-opportunity questions from it, in the editorial’s own style (“How should…”, “When does…”, “What governance structures…”).
3. Check each question: would a practitioner recognize their problem in it, or has it already drifted toward something only a researcher would ask?

20:00

Discussion

What insights for practice do you expect from your review?

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.

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.

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:

1. Your specific domain.
2. The important phenomenon within it.
3. 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.

Q&A

Footnotes

1. Grand challenges are large, important, unsolved problems, reflected for instance by the United Nations’ Millennium Development Goals to eradicate global poverty, disease, and hunger.

2. Adding to a conversation requires knowing the conversation. Research topics come from reading extensively in the literature.

3. According to Colquitt & George (2011), such topics arouse more interest than the more typical “gap-spotting” approach to generating research questions.