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)
Introduction
What is research?
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 communicating the results of research, that is telling a relevant story.
The relevance of your story is dependent on the phenomena that wish to explain or predict.
Thus, we start with discussing what a good topic is and outline 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 research 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
Colquitt and George (2011) put forth five distinct criteria for effective topics in information systems (IS) and management science:
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
Novelty
Changing the conversation
- Consider whether your study might change 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 area by investigating how knowledge capabilities of industry incumbents affected the generation, development, and performance of “spin-outs”
- Familiarity and nearness trap
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Picking a topic that is too familiar and/or too close to the existing literature and, thus, might may only offer contributions that are not sufficiently different from existing perspectives.
- Maturity trap
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Selecting a topic that is too mature and, thus, might 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 (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.
Scope
Casting a wider net (not easily applicable for your master thesis)
- 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
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
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.
Indications of bad research questions
Recker (2021) outlines for main problems indicating that research questions should be revised:
- 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” problem: You ask (too) many questions instead of one.
Further categories of inappropriate research questions are (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.
Good research questions
A good research question should be:
- Clear and focused: the question should clearly state what you need to do.
- Not too broad and not too narrow: it must be possible to answer the question within the constraints of your research.
- Not too easy to answer: the answers should not be obvious or affirmative.
- Researchable: you must have access to data required to answer the question.
- Analytical rather than descriptive the question should allow you to produce an analysis of the problem rather than a simple description of it.
Once you have identified an important phenomenon, you need to engage with literature to identify problems with the existing knowledge. This helps you to narrow down your topic and create a good research question.
Research questions are typically one of two types based on the issues they address (Recker 2021):
- “What,” “who,” and “where” questions tend to focus on issues we seek to explore or describe because little knowledge exists about them.
- “How” and “why” questions are explanatory as they seek to answer questions about the causal mechanisms that are at work in a particular phenomenon.
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?
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?
Literature
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↩︎