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:

Describing some phenomena that we perceive in the world
articulating a theory to account for the phenomena; and
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.

We will discuss some criteria and tools that may help you to find and chose a phenomena that creates momentum and is worth to devote your scarce resources.

Effective topics

Focus areas

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

What is the anatomy of a topic in information systems and management studies that creates momentum?

In an attempt to answer that question, Colquitt and George (2011) put forth five distinct 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”

Familiarity, maturity, and nearness traps

Familiarity trap: Picking a topic that is too familiar and, thus, might only offer marginal extension of an existing conversation. (“familiarity trap”)
Maturity trap: Selecting a topic that is too mature and, thus, might only offer redundant contributions.
Nearness trap: Choosing a topic that is too close to the existing literature and, thus, may only offer contributions that are not sufficiently different from existing perspectives.

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.

Other categories of inappropriate research questions (Recker 2021):

Obvious questions: “Are there challenges in using information technology?” Of course there are. Obvious questions have answers to which everyone would agree.
Irrelevant questions: “What is the influence of weather on the salaries of technology professionals?” There is no reason to believe that there is any influence whatsoever.
Absurd questions: “Is the earth flat after all?” Absurd questions have answers to which everyone would agree, although I read that almost two percent of people still believe the earth is flat.
Definitional questions: “Is technology conflict characterised by disagreement?” The answer is simply a matter of creating a concept that says it does. A definition is a form of description, not research.
Affirmation questions: “Can a decision-support tool be developed to facilitate decision-making for senior retail executives?” Yes.

Use the problem statements to check your research questions and the above categories as an exclusion list to ensure that your proposed research questions do not fit any of these problems, and if they do, go back and revise them.

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?

Example

Recker (2021, 36 ff) uses following example on the motivation of a research question:

Organisations invest heavily in new information technology to seek benefits from these investments.

In this statement, we learn about a problem domain: investments into IT and benefit realisation from IT. This is an important problem domain for businesses because it involves money. As a tip, motivating research problems by citing data that confirm the quantifiable value associated with the problem (dollars spent, money lost, for example) might be valuable. Within this domain, we then learn about one important phenomenon:

Many of these benefits never materialise because employees do not use the technologies.

Here we drill down to a particularly important phenomenon of interest, individuals’ rejection of IT (i.e., their unwillingness to use IT), which narrows the problem domain down and will be useful in focussing the research later on. Finally, we learn about an important problem in the available knowledge that relates to this phenomenon:

The literature to date has studied only why individuals accept new technologies but not why they reject them.

Here we make a statement about the current body of knowledge. The problem with the body of knowledge we have (i.e., the literature available to date) is that it has a gap—that is, we do not know enough yet to address the specific phenomenon in the problem domain. For example, as the Covid-19 pandemic spread across the globe in 2020, at the beginning we had very little knowledge about the virus, its infection rates, and its possible cures or vaccinations. The problem then was a gap of knowledge.

A “gap” in knowledge is a typical problem with the available knowledge, but it is not necessarily the best or only problem (Alvesson and Sandberg 2011). For example, we could develop a set of arguments to strengthen the proposition that our theories on technology acceptance (e.g., Venkatesh et al. 2003) fail to predict the opposite, rejection of technology, conclusively. Other typical problems with the knowledge could be that they have yielded inconsistent results: study A suggests one thing and study B suggests an opposite thing, so which is correct? That is a problem. Another problem might be that the knowledge to date rests on assumptions that are no longer current or realistic, such as when studies assume that findings for a sample of men must also apply to women.

Having introduced an important problem domain with a specific phenomenon and a substantial problem with the knowledge to date allows us to formulate a research question as the logical conclusion to these arguments:

Why do people reject new information technology?

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

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