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Andy Weeger / Neu-Ulm University of Applied Sciences Neu-Ulm / Academic Writing (Master)

Topic choice

How to find a topic that creates momentum?

Andy Weeger

Neu-Ulm University of Applied Sciences

January 1, 2022

Motivation

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)

Exercise

Read the MISQ editorial of Weber (2003) and summarize what you have learned about the challenge of choosing a topic for your research (approx. 20 minutes).

Introduction

Main activities

Weber (2003) characterizes doing research in terms of three activities:

  1. Describing some phenomena that we perceive in the world
  2. articulating a theory to account for the phenomena; and
  3. testing how well the theory accounts for the phenomena.

In this course, we will not focus on the skills required for good research design or theory-building, rather we focus on telling a relevant story.

How relevant the story is, is defined in the first phase of research, which is about describing those phenomena that you perceive in the world that you wish to explain or predict.

Effective topics

Focus areas

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

Criteria for effective topics

Significance, novelty, curiosity, scope, and actionability

Significance

Taking on “grand challenges”

  • Identify and confront or contribute to a grand challenge1
  • Tackle such problems in a particular area if inquiry (i.e., slicing the elephant)
  • Aim at a contribution that has theoretical usefulness and from which individual and societal benefit may accrue
  • Take a bold and unconventional way that leaps beyond existing explanations (e.g., going behind conventional 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

Exercise

What “grand challenges” do you see?

In which area if inquiry could (your) research contribute to it?

Novelty

Changing the conversation

  • Consider whether your study changes the conversation that is already taking place in a given literature2
  • Aim at either adding momentum to a conversation or giving it a new direction
  • Think of how you can generate new and creative solutions by exploring new domains and not to prefer the familiar, the mature and perspectives that are near to existing approaches (i.e., avoid the familiarity, maturity, and nearness traps)

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

Exercise

What strategies can you apply to identify a topic that that avoids the familiarity, maturity, and nearness traps?

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 (i.e., “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.

Exercise

What are “mysteries” you have identified in your literature work?

Scope

Casting a wider net

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

Example: Seibert, Kraimer, and Liden (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

Exercise

What would be a relevant perspectives for your study?

Actionability

Offer insights for managerial or organizational practice

McGahan (2007) outline 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

What insights for practice do you expect from your study?

Conclusion

An effective topic …

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

Research question

Importance

Once you have identified a problem domain with an important phenomenon that deserves attention and relates to an problem with existing knowledge (i.e., an effective topic), you need to formulate and develop your own research questions and propose a plan to address them.

This challenge is much more difficult than learning methods and theories, largely because it is not as structured but is undefined and highly contextual (Recker 2021).

However, the research question(s) is/are the fundamental cornerstone that around which your whole research project revolves and evolves.

Four problem indications

The “monologuing” problem

You cannot tell what research question your are tackling unless you engage in a five-minute monologue—you have not grasped the essence of the problem yet.

The “so what” problem

You cannot tell why answering the research question matters to anyone.

The “solving the world” problem

Your question has value, but cannot be answered given your resource constraints.

The “multitude”

You ask (too) many questions instead of one.

Guiding questions

Recker (2021, 35–36) proposes a number of guiding questions can help you find a good research question, e.g.:

  • Do you know in which field of research your research questions reside?
  • Do you have a firm understanding of the body of knowledge in the field?
  • What are important open research questions or unsolved problems in the field that scientists agree on?
  • What areas need further exploration?
  • Could your study fill an important gap in knowledge?
  • Has your proposed study been done before? If so, is there room for improvement or expansion?
  • Is the timing right for the question to be answered?
  • Who would care about obtaining an answer to the question?

Exercise

Test your ideas about a possible research question.
Does it meet the criteria presented?

Q&A

Literature

Agarwal, Rajshree, Raj Echambadi, April M Franco, and Mitrabarun B Sarkar. 2004. “Knowledge Transfer Through Inheritance: Spin-Out Generation, Development, and Survival.” Academy of Management Journal 47 (4): 501–22.
Alvesson, Mats, and Jörgen Sandberg. 2011. “Generating Research Questions Through Problematization.” Academy of Management Review 36 (2): 247–71.
Colquitt, Jason A, and Gerard George. 2011. “Publishing in AMJ—Part 1: Topic Choice.” Academy of Management Journal. Academy of Management Briarcliff Manor, NY.
Ferlie, Ewan, Louise Fitzgerald, Martin Wood, and Chris Hawkins. 2005. “The Nonspread of Innovations: The Mediating Role of Professionals.” Academy of Management Journal 48 (1): 117–34.
McGahan, Anita M. 2007. “Academic Research That Matters to Managers: On Zebras, Dogs, Lemmings, Hammers, and Turnips.” Academy of Management Journal 50 (4): 748–53.
Recker, Jan. 2021. Scientific Research in Information Systems: A Beginner’s Guide. Springer Nature.
Seibert, Scott E, Maria L Kraimer, and Robert C Liden. 2001. “A Social Capital Theory of Career Success.” Academy of Management Journal 44 (2): 219–37.
Van Kleef, Gerben A, Astrid C Homan, Bianca Beersma, Daan Van Knippenberg, Barbara Van Knippenberg, and Frederic Damen. 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): 562–80.
Venkatesh, Viswanath, Michael G Morris, Gordon B Davis, and Fred D Davis. 2003. “User Acceptance of Information Technology: Toward a Unified View.” MIS Quarterly, 425–78.
Weber, Ron. 2003. “Editor’s Comments: The Problem of the Problem.” MIS Quarterly 27 (1): 7.

Footnotes

  1. The grand challenges are large, important unsolved problem. Current grand challenges might be reflected by the United Nations Millennium Development Goals to eradicate global poverty, disease, and hunger.

  2. Adding to a conversation requires to know the conversation. Research topics (and research questions), thus, do not come out of the air, you need to read a lot.

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