03 · What You Need to Know
Not Every Important Problem Is Automatically an Important Research Problem
Start by separating the practical problem from the research problem
A practical problem describes a condition someone wants to change. A research problem identifies something important that is not adequately known, explained, tested, measured, or understood.
They often overlap. They are not the same thing.
Practical problem
Something in a real setting requires improvement, prevention, management, explanation, or a decision.
Research problem
An important uncertainty in knowledge or evidence that systematic investigation can help resolve.
Suppose a university discovers that students wait too long for technical-support responses. The practical problem is clear: response times are unsatisfactory.
But do researchers need a study to establish that reducing an unnecessary delay would be desirable? Perhaps not.
The organization may simply need to analyze its workflow and change staffing or procedures. Calling the situation a research problem does not make research necessary.
Sometimes you already know enough to act
A common mistake is assuming that every important organizational or social problem needs another study before anyone can respond.
Imagine that a department has overwhelming evidence that students cannot access a required laboratory because its opening hours conflict with their scheduled classes. The problem is documented, the mechanism is obvious, and the solution is administratively feasible.
Conducting a survey to determine whether students would prefer more accessible hours might add little.
The academically difficult question is: what remains uncertain enough to justify systematic investigation?
If the answer is “nothing important,” the responsible response may be action rather than research.
Watch Out
Do not manufacture a research gap simply because an important problem exists. If adequate evidence already identifies the cause and supports a reasonable response, another study may delay action without producing knowledge that changes the decision.
Research and problem-solving are overlapping but different activities
Research is one way of responding to practical problems. It is not the only one.
An organization can redesign a process, repair a system, train staff, consult users, audit performance, implement an established intervention, or apply existing evidence without attempting to generate a scholarly contribution.
Research becomes more compelling when uncertainty itself is part of the problem.
Perhaps nobody knows why the process fails. Several plausible interventions exist, but their relative effectiveness is uncertain. Evidence from other settings may not transfer because an important contextual condition differs. A widely used solution may rest on weak evidence. Implementation may repeatedly fail despite apparently sound interventions.
Now systematic investigation can potentially produce both practical and intellectual value.
A problem can be locally important but academically saturated
Suppose employees in one organization experience a familiar workplace problem that has already been investigated extensively across comparable settings using strong research designs.
The organization may still need to address it. It may even need local data to determine the scale of the problem or select among available responses.
But another study asking whether the already well-established problem is associated with the already well-established outcome may contribute little to scholarship.
This is where practical importance and marginal academic contribution diverge.
The local study could still be valuable for organizational decision-making. If the aim is academic publication, however, you need to explain what uncertainty remains beyond confirming that the familiar relationship also appears in one more organization.
The question resembles the issue examined in deciding whether a local research question has broader value. Local importance can justify evidence gathering without automatically establishing a broader scholarly contribution.
“Nobody has studied our organization” is rarely enough
A practical problem can make geographical or institutional novelty feel more persuasive than it actually is.
Suppose workplace burnout is causing serious problems at Organization X. You discover extensive research on burnout but no published study specifically involving Organization X.
That absence does not by itself create an academic gap.
The organization may need local evidence because its leaders cannot responsibly assume that prevalence estimates from elsewhere describe their employees. That is a legitimate local evidence need.
For broader academic justification, however, ask what studying this setting contributes. Does the organization have an unusual workload structure? Has it implemented a policy that provides a natural comparison? Does its workforce differ in theoretically relevant ways? Does existing evidence fail under similar organizational conditions?
The contribution comes from what the setting allows you to learn, not from the fact that its name has never appeared in a journal article.
A practical need can justify local research even without a large academic contribution
Academic contribution is not the only legitimate reason to collect evidence.
WHO's guidance on research priority setting, for example, emphasizes public need, implementation and end-user considerations, stakeholder involvement, feasibility, and potential public health benefit when setting priorities. It also recognizes that research resources are scarce and that prioritization involves judgments about where potential benefits should be directed.
That logic illustrates a broader point. A decision-maker may reasonably need context-specific evidence even when the resulting study does not substantially change an academic field.
If a hospital needs reliable local evidence to allocate a scarce service, or a university needs to determine whether an intervention is working for its own students, producing that evidence can be worthwhile.
The important editorial decision is to describe the contribution accurately. A locally valuable study does not need to pretend it will transform general theory.
Practical significance and academic significance can coexist
The choice is not always between research that advances knowledge and research that solves problems.
Donald Stokes' influential framework, often called Pasteur's Quadrant, separates the quest for fundamental understanding from considerations of use. The National Academies has used this framework to describe use-inspired basic research: work that seeks fundamental understanding while also being motivated by practical use.
This is useful because it breaks the simplistic assumption that a researcher must choose between academically interesting questions and practically useful ones.
| Primary orientation |
Possible research contribution |
| Fundamental understanding without immediate use |
Develop theory, explanation, concepts, or foundational knowledge |
| Practical use with limited fundamental ambition |
Evaluate or develop a solution for a particular practical need |
| Use-inspired fundamental inquiry |
Address a practical problem while investigating mechanisms or principles with broader explanatory value |
The categories should not be treated as rigid boxes into which every study must fit. Their value is conceptual: practical motivation and academic contribution can be separate dimensions rather than opposite ends of one scale.
Move from “How do we fix this?” to “What do we need to understand?”
When a practical problem is academically thin, one productive move is to identify the uncertainty underneath it.
Suppose a university has low completion rates in online courses.
“How can we increase completion?” is an important practical question, but it is too broad to function as a useful research question.
Ask instead what prevents an evidence-based response.
Do students leave for different reasons at different stages? Does a widely used model of persistence adequately explain departure in asynchronous programs? Are administrative indicators failing to identify the students most likely to disengage? Does a support intervention work only for particular types of learners?
Now the practical problem motivates questions whose answers can potentially improve both local action and broader understanding.
Mechanism can connect a local problem to a broader contribution
One particularly useful bridge is mechanism.
Instead of asking only whether a problem occurs, investigate how or why it occurs.
Suppose an institution finds that students rarely use optional instructor feedback. A purely local study might estimate how many students use it. That could be useful for management.
A broader research question might investigate whether perceived cost, trust, timing, feedback literacy, or another process explains students' decisions to engage with feedback.
If the proposed mechanism connects with existing theory and can be examined beyond the immediate institution, the study may contribute knowledge while remaining motivated by the local problem.
The practical problem gives the research urgency. The mechanism gives it explanatory reach.
Testing an intervention can create an academic contribution when genuine uncertainty remains
Another bridge is comparative effectiveness.
Suppose an organization has identified three plausible ways to address a problem, and existing evidence does not establish which is most effective under the relevant conditions.
A well-designed comparison may answer a practical decision while also contributing evidence about intervention effectiveness, heterogeneity, mechanisms, implementation, or contextual boundaries.
The contribution becomes weaker when the intervention's effectiveness is already well established under highly comparable conditions and the new study merely repeats the comparison without addressing remaining uncertainty.
Again, the existence of the problem does not determine the research contribution. The unresolved evidence does.
Implementation failure can itself become an important research problem
Sometimes researchers know that an intervention can work, yet organizations repeatedly struggle to implement it effectively.
The practical question then shifts.
Instead of asking, “Does the intervention work?”, the more informative question may be, “Why does an evidence-supported intervention fail to produce the expected outcome under these implementation conditions?”
This can open questions about fidelity, adaptation, organizational readiness, professional behavior, resources, acceptability, or interactions between intervention and context.
Such questions may have broader relevance because many organizations face the gap between evidence of efficacy and effectiveness in practice.
NIH's Science of Behavior Change initiative, for example, has explicitly discussed gaps between basic and applied research and between intervention efficacy and effectiveness, using use-inspired basic research as one way to investigate mechanisms within applied research contexts.
A practical problem may expose a weakness in existing theory
Real-world problems can also reveal phenomena that established theories explain poorly.
Suppose a widely used model predicts that students with particular characteristics should respond positively to an intervention, but practitioners repeatedly observe the opposite under certain conditions.
Rather than treating practice merely as the place where theory is applied, the discrepancy can become a theoretical problem.
Why does the expected relationship fail? Is an important contextual variable missing? Does the mechanism operate differently? Has the theory been extended beyond the conditions under which it was developed?
The practical anomaly becomes academically useful because it tests the adequacy of existing explanation.
A practical problem may need evaluation rather than research
Not every systematic investigation needs to be framed as research intended to contribute generalizable or transferable knowledge.
An organization may primarily need to determine whether its own program met its objectives. That is often an evaluation question.
A university might ask whether a tutoring program reached its intended students, whether participants were satisfied, whether implementation matched the program design, and whether target indicators improved.
Those questions can be rigorous and consequential. Their primary purpose, however, may be judging or improving that specific program rather than producing new academic knowledge.
The boundary between research and evaluation can vary by context, purpose, methodology, institutional policy, and ethical or regulatory framework. Researchers should not assume that calling a project “evaluation” removes applicable ethical or governance requirements.
The useful point here is simpler: academic publication is not the only legitimate destination for systematic evidence gathering.
Some problems call for quality improvement rather than another explanatory study
A similar distinction arises with quality improvement.
Suppose a hospital knows from reliable internal data that a particular administrative process creates avoidable delays. The organization has an evidence-supported alternative and wants to implement it, monitor performance, and refine the process.
The central need may be improvement rather than new knowledge.
Trying to convert every improvement activity into academic research can create unnecessary complexity and sometimes distract from the people who need the problem fixed.
Research becomes more compelling when the improvement effort raises an unresolved question whose answer could inform knowledge beyond routine monitoring of the change.
A practical problem can be too context-dependent for the academic claim you want to make
Some practical problems arise from highly specific organizational arrangements.
Imagine a university experiencing registration delays because three internal databases use incompatible identifiers. Solving the problem may be extremely important to the institution.
But a detailed study showing that incompatible identifiers cause delays may have limited academic value if the causal chain is already obvious and the configuration is unique.
That does not mean nothing can be learned from the case. Perhaps the broader question concerns interoperability, organizational coordination, or technology governance. But the researcher must establish that connection rather than assuming it.
A local inconvenience does not become a general phenomenon simply because the paper describes it abstractly.
The practical problem may be important while your proposed outcome is not
Another common mismatch occurs when researchers begin with a serious problem but measure whatever outcome is easiest.
Suppose employee turnover is costly and disruptive. Instead of studying actual turnover, retention behavior, or mechanisms closely connected to leaving, a researcher measures general attitudes because a convenient questionnaire is available.
The practical importance of turnover does not automatically transfer to every variable statistically associated with it.
This is an important diagnostic:
Does answering my specific research question actually inform the practical problem I use to justify the study?
If not, the problem may be serving as rhetorical background rather than as the phenomenon the research genuinely addresses.
A practical problem may be too broad for one study
“Improve education.” “Reduce poverty.” “Fix misinformation.” “Improve healthcare access.” “Prevent employee burnout.”
These are important objectives, but they are not research questions.
A single study usually addresses one uncertainty within a much larger practical problem.
Researchers sometimes overstate their contribution because they describe the societal problem at enormous scale and then imply that their narrow study inherits that importance automatically.
It does not.
The practical problem establishes context. The importance of the research question depends on whether resolving the particular uncertainty moves understanding or action forward in a meaningful way.
Watch Out
Do not borrow the importance of a large social problem for a small research question without explaining the connection. Studying one minor predictor of a major problem does not automatically make the predictor important. Show how the knowledge your study produces bears on the problem you invoke.
Stakeholders can help reveal whether the research question addresses the actual problem
Researchers sometimes conceptualize practical problems from the outside and assume they understand what information practitioners or communities need.
Research-priority guidance from WHO emphasizes engagement with a wide range of stakeholders and incorporation of implementation and end-user needs. Its 2025 ethics guidance also stresses that research priority setting involves value judgments about whose interests count and how scarce research resources and potential benefits are distributed.
The principle applies more broadly than health research.
If your study is justified by a practical problem, speaking with people who experience, manage, or make decisions about that problem can reveal whether your proposed question is actually useful.
They may identify constraints you overlooked, outcomes that matter more than those you planned to measure, or questions that researchers find intellectually appealing but practitioners do not need answered.
Stakeholder priorities should not automatically dictate the scientific agenda. They are evidence about practical relevance.
Feasibility and opportunity cost matter when practical needs compete
A problem can be important yet still not be the research project you should pursue.
WHO's research-priority guidance emphasizes that priorities involve balancing potential benefit with scientific feasibility and the resources required. Its more recent ethics guidance makes the opportunity-cost problem explicit: money, personnel, infrastructure, and time devoted to one project cannot simultaneously be used for another.
This is relevant even outside formal priority-setting exercises.
If answering a narrow practical question requires three years, substantial funding, and burdensome data collection while existing evidence already supports a reasonable intervention, direct action or a smaller evaluation may be more defensible.
Conversely, a difficult study may be justified when the unresolved uncertainty has major consequences and current action rests on weak evidence.
Use-inspired research can produce both understanding and use
The most productive response to an academically thin practical problem is not always to make it more theoretical.
Sometimes the better strategy is to formulate a question that genuinely pursues understanding while remaining anchored in use.
National Academies discussions of Stokes' framework describe use-inspired basic research as simultaneously seeking fundamental understanding and responding to practical concerns. In discipline-based education research, for example, research can range from fundamental studies of learning and cognition to applied studies of instructional effectiveness, with many questions combining both orientations.
A practical educational problem might therefore motivate research into a mechanism of learning. A healthcare implementation problem might expose a broader question about professional decision-making. A technology failure might reveal a general issue in human-system interaction.
The practical setting does not merely provide participants. It becomes a place where a broader scientific question can be examined.
But do not force theory into a project merely to make it publishable
There is an opposite mistake.
Researchers sometimes attach a theoretical framework to a straightforward local evaluation because they believe academic research must contain theory. Variables are added, conceptual diagrams become increasingly ornate, and the original practical question becomes difficult to recognize.
Theory is useful when it helps explain the phenomenon, generate informative predictions, connect the case to existing knowledge, or reveal what should be measured.
It is not useful when it functions primarily as academic decoration.
If the project is fundamentally a local evaluation, calling it that may be more intellectually honest than forcing it to perform as a theory-testing study.
Practical relevance is not a substitute for research quality
An urgent problem can create pressure to accept weak evidence because “something must be done.”
But the importance of a problem does not make an inappropriate design capable of answering the question.
If a causal claim requires a credible comparison, urgency does not remove that requirement. If a construct needs valid measurement, practical importance does not rescue an unsuitable questionnaire. If a sample cannot support the intended population inference, the seriousness of the problem does not make it representative.
A weak study of an important problem can be less useful than a narrower study that answers a well-defined question credibly.
Practical importance can be enough for some purposes
Academic contribution should not become a universal gatekeeper for every evidence-generating activity.
An institution may commission research because it needs an answer. A government agency may require evidence for a policy. A community may want systematic documentation of an issue that directly affects its members.
In such cases, usefulness to the intended audience may be the principal criterion.
The question becomes academically difficult mainly when the project is simultaneously expected to contribute to scholarly literature, satisfy a dissertation's originality requirements, compete for research funding, or make claims beyond the immediate case.
Different purposes legitimately impose different standards.
The academic contribution may be smaller than the practical contribution
Researchers sometimes feel compelled to make both dimensions equally impressive.
They do not need to be.
A study might have enormous value to one organization while adding a modest but defensible piece of evidence to the literature. Another might make a substantial theoretical contribution while offering little immediate practical benefit, as discussed in the guide on academically interesting but practically unimportant research.
Contribution profiles differ.
The important editorial task is to describe them accurately rather than inflate whichever dimension appears weaker.
Ask what the study teaches beyond “we have this problem”
A practical problem becomes a stronger academic research opportunity when the study can answer a question whose significance extends beyond documenting the problem's existence.
That broader lesson might concern:
- why the problem occurs;
- which mechanism produces it;
- which intervention works and under what conditions;
- why an established intervention fails during implementation;
- which contextual feature changes the expected relationship;
- how the phenomenon should be measured;
- which theoretical explanation better accounts for it;
- how findings from previous settings need to be qualified.
You do not need all of these. One meaningful uncertainty is enough if it is the right one.
The practical problem supplies a reason to care. The research problem supplies something worth learning.
