01 · The Question
Is a Problem More Worth Studying When Research Could Actually Change It?
Suppose two problems are equally serious. One appears highly changeable: better evidence could plausibly lead to an intervention, policy, design, or practice that reduces the problem. The other has no obvious solution, and even excellent research may not produce an immediate way to prevent or reduce it.
Should the first problem receive greater research priority?
Often, its changeability strengthens the case. Research resources are limited, so the prospect that new knowledge could produce meaningful benefits is relevant. But making preventability a requirement would create another problem. Many major advances begin with research on phenomena that researchers cannot yet prevent, treat, or control. Sometimes the purpose of research is precisely to make a previously intractable problem changeable.
03 · What You Need to Know
Research Priority Depends on What Knowledge Could Make Possible
Preventability and Changeability Are Related but Not Identical
A preventable problem is one whose occurrence can potentially be reduced or avoided. A changeable problem is broader. Research may not prevent the problem itself but could reduce its severity, improve detection, alter its consequences, improve adaptation, change how institutions respond, or help affected populations manage it more effectively.
This broader concept matters because "Can we eliminate it?" is often too demanding a test. Research can have considerable value without making a problem disappear.
Preventability
The extent to which the occurrence of a problem could potentially be avoided or reduced.
Changeability
The extent to which research-informed action could alter the problem, its causes, consequences, management, detection, or the conditions surrounding it.
Why Changeability Can Strengthen Research Priority
Research priority is partly about the expected return from producing knowledge. WHO's guidance for research priority setting groups potential public health benefit among the broad dimensions that can be considered alongside scientific feasibility and cost. Its research-agenda guidance similarly emphasizes public need, feasibility, implementation, and the potential for research to contribute to impact.
If a problem is serious and evidence could plausibly lead to a substantial improvement, that connection strengthens the case for investing research resources. The reasoning is straightforward: the study has a credible pathway from unanswered question to useful knowledge and from useful knowledge to possible benefit.
This does not mean that every study must produce an intervention. It means that the expected consequences of obtaining the answer belong in the priority judgment.
Current Lack of a Solution Can Make Research More Important, Not Less
There is an obvious danger in prioritizing only problems that already look tractable. Problems with straightforward solutions would repeatedly attract resources, while difficult problems could remain difficult precisely because comparatively little research is directed toward them.
Basic and exploratory research often begins before researchers know whether practical change is possible. Investigating mechanisms, causes, structures, or processes may create options that cannot be anticipated at the outset.
A problem that is currently resistant to intervention may therefore have high research value if reducing fundamental uncertainty could change what becomes possible later. This is particularly relevant when the problem is severe and existing options are inadequate.
Watch Out
Do not confuse "we do not currently know how to solve this" with "research cannot help." The first describes the present state of knowledge. The second is a much stronger claim that requires evidence.
Tractability Can Refer to the Research Question Rather Than the Entire Problem
A large social, scientific, or practical problem may not be solvable by one study. That does not make it unresearchable. Researchers can identify a consequential component that is amenable to investigation.
For example, a researcher may be unable to eliminate educational inequality but could investigate a specific mechanism contributing to unequal access. A cybersecurity researcher may not be able to prevent every attack but could test a particular vulnerability. A health researcher may not be able to cure a condition but could improve diagnosis or symptom management.
The appropriate unit of judgment is therefore often the research question and its potential contribution, not whether the entire underlying problem can be solved.
Changeability Matters Most When Research Is Actually the Missing Ingredient
A problem may be highly preventable while additional research has little value. Suppose strong evidence already identifies an effective intervention, but organizations are not using it because of insufficient funding or lack of enforcement. The problem is technically changeable, yet another study establishing that the intervention works may accomplish little.
Conversely, an apparently intractable problem may contain a critical unanswered question that prevents progress. Research could have high expected value because reducing that uncertainty is a necessary step toward future change.
This is why knowing a likely solution changes the research question rather than automatically reducing the importance of the underlying problem .
Feasibility Is Not the Same as Changeability
Another distinction is necessary. A problem can be highly changeable in principle but difficult to study rigorously. Conversely, researchers may be able to investigate an unchangeable phenomenon very effectively.
Question
What It Evaluates
Can the problem be changed?
Whether meaningful improvement is possible.
Could research contribute to that change?
Whether new knowledge is an important missing ingredient.
Can the proposed question be studied?
Whether credible evidence can realistically be produced.
Would the expected improvement matter?
Whether the potential benefit is consequential enough to justify the research.
WHO's systematic approach to research priority setting similarly treats potential benefit, scientific feasibility, and resource cost as distinct dimensions. Keeping them separate prevents "changeable" from becoming shorthand for "easy to research."
Expected Benefit Depends on the Size of the Possible Change
Changeability is not simply yes or no. One problem may be almost completely preventable, another reducible by 10%, and another impossible to prevent but substantially manageable once it occurs.
The magnitude of realistic improvement matters. A small achievable improvement to a widespread or severe problem may have greater expected value than complete prevention of a trivial one.
That is why priority decisions should still consider severity and prevalence rather than treating tractability as the dominant criterion .
Equity Can Complicate a Pure Tractability Rule
Prioritizing the problems easiest to change may produce efficient short-term gains, but it can also leave populations with difficult, poorly understood, or expensive problems behind.
WHO's ethics guidance emphasizes that research priority setting distributes scarce potential benefits and therefore incorporates value judgments about fairness and whose interests count. A priority system concerned only with where improvement is easiest could systematically disadvantage groups whose problems are harder to address.
This does not mean feasibility or expected benefit should be ignored. It means that efficiency and fairness may sometimes pull in different directions, and the trade-off should be acknowledged rather than hidden.
Scientific Value Can Exist Without Immediate Change
Some research is valuable because it improves explanation, theory, measurement, prediction, or foundational understanding. Immediate preventability is therefore a poor universal criterion for scientific importance.
This distinction is especially relevant when a problem has substantial scientific importance before its practical implications are obvious . The pathway from research to benefit can be indirect and uncertain without being nonexistent.
04 · A Practical Example
When the Easier Problem Is Not Automatically the Better Research Priority
Hypothetical Example
Two Problems in Digital Learning
Imagine a research team choosing between two problems in online learning. Problem A is a common interface problem that causes students minor inconvenience. Its cause is known, and a straightforward design change could almost completely eliminate it. Problem B is a much more serious accessibility problem affecting a smaller population, but researchers do not yet understand why it occurs and no reliable solution exists.
Problem A is highly changeable An established correction already exists.
But the research need is small The important knowledge required for change has already been produced.
Problem B is currently less changeable There is no established intervention because the underlying mechanism remains uncertain.
But the research need is substantial Understanding the mechanism may be necessary before an effective response can be developed.
Research priority Problem B may reasonably receive greater research priority even though Problem A is easier to fix.
The distinction is between a problem that is changeable and a problem for which research is needed to create change. Problem A may deserve immediate action. Problem B may deserve investigation.
Now suppose researchers already understand Problem B thoroughly and have strong reasons to believe no proposed study could materially improve understanding or available responses. Its severity would remain important, but the argument for the particular research project would weaken.
06 · What This Means for You
Ask What Research Adds to the Possibility of Change
When evaluating a research problem, do not ask only whether something can be done about it. Ask whether new knowledge is necessary for something better to be done.
This shifts attention from tractability in the abstract to the contribution of your proposed study.
A simple decision framework
If the problem is changeable but the required evidence already exists
Determine whether implementation rather than additional research should receive priority.
If the problem is changeable but the best response remains uncertain
Research may have high value because evidence could directly improve action.
If the problem is currently difficult to change because its causes are poorly understood
Investigate whether reducing fundamental uncertainty could create future options.
If prevention is impossible but consequences can be reduced
Evaluate the potential value of research on mitigation, management, adaptation, or support.
If no plausible pathway exists from the proposed research to meaningful knowledge or benefit
Reconsider whether the question warrants priority relative to stronger alternatives.
A research problem does not have to promise a solution. It should, however, offer a defensible reason for believing that the knowledge produced is worth obtaining.
07 · A Quick Checklist
Before Prioritizing a Problem Because It Can Be Changed
Before using changeability as a priority criterion, check:
Define what meaningful change would look like: prevention, reduction, mitigation, diagnosis, management, adaptation, or another outcome.
Determine whether credible interventions or responses already exist.
Identify whether lack of knowledge is actually preventing improvement.
Estimate how consequential the realistically achievable improvement could be.
Distinguish the feasibility of conducting the study from the changeability of the underlying problem.
Consider whether foundational research could create future options even when immediate change is unlikely.
Examine whether prioritizing only tractable problems would systematically neglect populations with difficult unmet needs.
Compare the expected value of the proposed research with alternative uses of the same resources.
11 · Cite this Guide
How to Cite This Guide
This guide is intended to be read, shared, and used in research, teaching, and academic work. If you draw on its ideas, explanations, or other content, please acknowledge the source by citing the guide. Doing so gives appropriate credit and helps your readers locate the original resource.
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