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, 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 (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 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
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, pp. 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?
Motivation of RQs
Recker (2021, p. 36 ff) proposes a systematic four-step approach for motivating research questions that ensures logical flow from broad context to specific inquiry.
First, establish a problem domain statement that highlights an important business or organizational context, emphasizing the scale and significance of the domain while including quantifiable evidence when possible, such as dollar amounts invested or lost, percentages of organizations affected, or market size metrics.
Second, identify a specific phenomenon by narrowing down from the broad domain to a particular issue or challenge, focusing on what makes this phenomenon especially important or problematic within the larger context.
Third, articulate the knowledge gap or problem by clearly stating what is wrong with current knowledge—this could be a gap where we don’t know enough about a topic, inconsistencies where studies show conflicting results, outdated assumptions where current theories rest on unrealistic premises, or limited scope where existing research only covers part of the phenomenon.
Finally, formulate the research question as a logical conclusion flowing from the previous three steps, ensuring it directly addresses the identified knowledge problem and is positioned to fill the gap or resolve the inconsistency identified in the literature.
Example #1 (Benlian et al., 2025)
Problem domain statement
Organizations increasingly adopt agile software development practices to improve project outcomes and developer productivity, with 71% of organizations now using agile practices in their software development lifecycle.
This establishes an important problem domain involving significant organizational investment in agile methodologies. The quantifiable aspect (71% adoption rate) demonstrates the widespread business relevance and financial implications of agile practices implementation.
Specific phenomenon
Despite this widespread adoption, agile projects continue to suffer from alarmingly high failure rates (50-96%), often attributed to human-related challenges where developers experience imbalances between the team-enacted use of agile practices and their individual needs for such practices.
This narrows down to the specific phenomenon of interest: the disconnect between how agile practices are implemented at the team level versus what individual developers actually need, leading to developer stress, reduced well-being, and project failures.
Knowledge gap/problem
The literature to date has implicitly assumed that developer needs are perfectly reflected in team-enacted agile practices, focusing primarily on the extent of agile practices use in teams while overlooking the critical dimension of individual developer needs and the potential for incongruence between team practices and personal requirements.
This identifies the gap in existing knowledge - previous research has adopted a one-dimensional view of agile practices use, assuming perfect alignment between team implementation and individual needs, without considering how misalignment affects developer outcomes.
Research questions
How do daily congruence and incongruence in the team-enacted versus individually needed use of agile practices affect developer well-being? Additionally, how pronounced is the influence of this congruence and incongruence among frequent (versus infrequent) team feedback-seeking developers?
This research question logically follows from the identified problem domain, specific phenomenon, and knowledge gap, addressing the need to understand the effects of (mis)alignment between team-level and individual-level agile practices use.
Example #2 (Strich et al., 2021)
Problem domain statement
Organizations are increasingly adopting artificial intelligence systems in the workplace to enhance efficiency and competitiveness, with AI systems becoming capable of autonomously performing complex decision-making tasks that were previously the exclusive domain of skilled professionals.
This establishes an important problem domain involving significant organizational investment in AI technologies. The business relevance is demonstrated by the widespread adoption across industries and the substantial impact on human work processes and organizational structures.
Specific phenomenon
However, when AI systems substitute for employees’ core professional activities—particularly decision-making responsibilities—employees must relinquish defining aspects of their work without the ability to interact with or influence the AI system, creating fundamental challenges to how they perceive themselves professionally.
This narrows down to the specific phenomenon of interest: the disconnect between employees’ professional identity and their actual work when AI systems take over their core responsibilities, particularly focusing on substitutive decision-making AI that eliminates human interaction possibilities.
Knowledge gap/problem
The literature to date has primarily focused on how employees interact with and adapt to new information systems, assuming that users can engage with, influence, or overrule technological decisions. However, little is known about how substitutive decision-making AI systems—which eliminate employees’ ability to interact with the technology—affect employees’ professional role identity and the mechanisms they develop to cope with this unprecedented challenge.
This identifies the gap in existing knowledge - previous research assumed human-technology interaction was possible, but substitutive AI systems represent a new class of technology that removes this interaction capability, creating unknown effects on professional identity.
Research questions
How does the introduction of a substitutive decision-making AI system affect employees’ professional role identity? And how do employees adapt their professional role identity in response to these AI systems?
This research question logically follows from the identified problem domain, specific phenomenon, and knowledge gap, addressing the need to understand both the effects of and responses to AI systems that fundamentally alter professional work without allowing human interaction or influence.
Homework
The research question is the fundamental cornerstone that around which your whole research project and your writing revolves and evolves.
Think about the phenomenon, go to literature, identify a relevant problem and draft candidate research question(s).
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 & George (2011) such topics arouse more interest than the more typical “gap-spotting” approach to generating research questions↩︎