03 · What You Need to Know
How a Practical Problem Becomes a Researchable Problem
Start by Describing the Problem Without Explaining It Away
A useful first move is surprisingly simple: describe the situation before deciding why it exists.
Suppose a community health program offers free appointments, but many eligible people do not attend. “Eligible people are not using the service at the expected rate” describes a discrepancy that may warrant investigation. “People do not attend because they do not understand the benefits” is already a causal explanation.
That explanation might eventually prove correct. It might also be wrong. Transportation, inconvenient scheduling, distrust, stigma, competing responsibilities, poor communication, eligibility confusion, previous experiences with the service, or other factors could be involved.
WHO's implementation research materials explicitly approach practical challenges this way: identify bottlenecks and relevant stakeholders, formulate research questions, conduct research, and use the findings to inform action. The toolkit's problem-analysis guidance asks researchers to examine discrepancies between actual and intended situations and consider multiple possible explanations rather than assuming a single cause.
A Real-World Problem and a Research Problem Are Related but Not Identical
A practical problem concerns a condition in the world that someone may want to change: low uptake, excessive delays, unequal access, recurring failure, poor retention, unexpected behavior, environmental degradation, inefficient processes, or another consequential situation.
A research problem identifies what about that situation needs investigation. Perhaps the causes are unclear. Perhaps an intervention works in one setting but not another. Perhaps stakeholders disagree about what the problem actually is. Perhaps a proposed solution has never been adequately evaluated.
Practical problem
Something in the world is happening, not happening, or producing outcomes that stakeholders consider important.
Research problem
Something relevant to understanding or addressing that situation remains uncertain, insufficiently explained, or inadequately tested.
Research question
A focused question states what the investigation will try to find out about that uncertainty.
This is one reason it helps to distinguish the topic, research problem, and research question. A practical concern can motivate all three without being interchangeable with them.
First Establish That the Problem Is Actually a Problem
Before investing months or years in explaining a problem, check whether your description of it is supported.
How large is the discrepancy between what is happening and what was expected? How many people or processes are affected? How serious are the consequences? Has the situation persisted long enough to distinguish it from ordinary variation? Who considers it a problem, and do other stakeholders see it differently?
WHO's implementation research guidance includes comparable considerations when prioritizing problems and questions, including how widespread or severe a problem is, who is affected, who considers it a problem, its burden, and whether the issue or question has already been researched.
The evidence you need depends on the subject. Administrative records, monitoring data, previous evaluations, interviews, observations, published studies, policy documents, or other sources may help establish the situation before you formulate a larger research project.
Ask Who Gets to Define the Problem
Real-world problems often involve multiple groups whose priorities do not perfectly align.
Hospital administrators may define a problem as excessive waiting time. Clinicians may see understaffing and workflow design as the central issue. Patients may care most about communication, uncertainty, cost, or whether the visit ultimately resolves their concern.
This does not mean every research project must satisfy every stakeholder equally. It does mean that problem definition should not automatically inherit the perspective of whoever has the most institutional authority.
Implementation research offers a useful illustration. TDR describes implementation research as demand-driven, with questions framed from needs identified by relevant stakeholders and implementers working within the health system. Research on implementation also emphasizes collaboration between researchers, decision-makers, frontline workers, patients, and other affected groups when translating practical challenges into researchable questions.
Find Out Whether the Answer Is Already Known
Not every operational difficulty requires new research. Sometimes the necessary knowledge already exists and the real challenge is applying it.
Imagine an organization discovering that staff routinely make a particular procedural error. If extensive evidence already identifies the cause and a well-supported corrective process exists, another exploratory study may add little. The organization may need implementation, training, resources, evaluation, or quality improvement rather than a new investigation of the same basic question.
Conversely, a proven intervention may work under controlled conditions but encounter barriers when implemented in routine settings. That itself can generate research questions about adoption, feasibility, acceptability, reach, context, sustainability, or implementation strategies. Implementation research specifically addresses questions about how evidence-informed interventions work in real-world settings and why implementation succeeds or fails.
Separate the Problem From Your Preferred Solution
People who encounter practical problems often arrive with solutions already in mind. A manager sees low productivity and proposes monitoring software. A university sees poor student attendance and proposes stricter attendance requirements. A city sees traffic congestion and proposes a particular transport intervention.
That can create a subtle research mistake: defining the study so that it evaluates only whether the preferred solution should be implemented rather than investigating whether the diagnosis behind that solution is sound.
Try writing the problem without mentioning the solution. If you cannot do so, you may have framed the situation too narrowly.
Watch Out
“How can we prove that intervention X will solve the problem?” is not an open research question. The wording has already assumed the intervention works. A defensible study should permit findings that challenge the proposed explanation or solution.
Decide What Kind of Knowledge Would Actually Help
A single practical problem can generate very different research questions because researchers may need different kinds of knowledge.
| If You Need To... |
You Might Ask... |
| Describe |
What is happening, to whom, where, and how often? |
| Explore |
How do affected people experience or understand the problem? |
| Explain |
What factors or mechanisms may account for the observed pattern? |
| Compare |
How does the problem differ across groups, settings, conditions, or approaches? |
| Evaluate |
Does an intervention produce the intended outcome, and under what conditions? |
| Understand implementation |
What barriers and facilitators affect adoption, delivery, reach, or sustainability? |
WHO's practical guide to implementation research similarly distinguishes questions intended to describe, explore, explain, influence, or predict. The purpose of the question helps determine what methods will be appropriate.
Do Not Make the Research Question Bigger Than the Problem Requires
Real-world problems can be enormous. “Food insecurity,” “traffic congestion,” “teacher shortages,” “misinformation,” and “climate adaptation” describe domains containing countless interacting problems.
A research project does not need to solve the entire domain. It needs to investigate a defensible part of it well.
Suppose a university experiences high dropout rates. A project attempting to discover “all causes of university dropout and how to eliminate them” is unlikely to be manageable. A more focused study might investigate how a particular group of students describes the factors influencing withdrawal during a defined stage of study, or evaluate whether a particular intervention affects retention under specified conditions.
The problem should guide how you narrow the research topic. Narrowing is useful when it creates a study that can produce meaningful evidence, not when it merely adds arbitrary boundaries.
Feasibility Can Change the Question Without Making It Unimportant
You may identify an important problem but lack access to the evidence required to investigate your preferred question.
A researcher studying workplace discrimination may not be able to access confidential personnel records. A researcher interested in emergency response may be unable to manipulate operational conditions experimentally. A student may identify a national policy problem but have time and resources for only a small, well-defined study.
The correct response is not necessarily to abandon the problem. You may need to ask a different question that contributes useful knowledge within realistic constraints.
This is where the relationship between the problem and the data you can actually access becomes consequential. Data availability should influence feasibility without becoming the sole reason a question exists.
Research Does Not Have to Produce an Immediate Solution
A study can be useful without ending with a ready-to-implement intervention. Sometimes the most valuable contribution is accurately defining the problem, identifying previously misunderstood barriers, testing an assumption, explaining variation, or establishing that a proposed solution does not work as expected.
Applied research is still research. The fact that stakeholders want actionable results does not eliminate requirements for appropriate design, transparent limitations, ethical conduct, and conclusions that match the evidence.
Likewise, not every research finding will transfer directly into policy or practice. Implementation depends on context, resources, values, feasibility, stakeholder priorities, and the strength and applicability of the evidence.
A Practical Problem Can Lead to Several Legitimate Studies
There is rarely only one research question hidden inside a real-world problem. Different disciplines and stakeholders may ask different questions about the same situation.
A decline in public-transport use could generate research on passenger behavior, service reliability, urban design, pricing, accessibility, environmental consequences, communication, or policy. Those studies are not interchangeable even though they originate from the same practical concern.
This is why starting with a problem can be productive without determining your study in advance. The problem establishes a reason to investigate; research development determines which part of that problem your project can credibly address.
