What Question Would Be Most Valuable to Answer Next?

If you could answer only one more research question, which should it be?

Research agendas usually contain more unanswered questions than there are resources to investigate them. Some topics have little evidence. Others have conflicting findings. Some uncertainties affect major decisions, while others are scientifically interesting but unlikely to change what anyone does.

This creates a different problem from simply finding a research gap. Once several legitimate gaps have been identified, which one deserves to be answered next?

The strongest candidate is not automatically the newest question, the largest gap, or the uncertainty with the widest confidence interval. Research priority depends on what could improve if the question were answered, how important that improvement would be, whether the uncertainty can realistically be reduced, and what must be spent or forgone to obtain the answer.

The most valuable question is the one whose answer can make the greatest worthwhile difference

Research prioritization asks what is most worth learning, not merely what remains unknown

A research gap identifies an opportunity, not a priority

Finding that something is unknown establishes a possible research question. It does not establish that answering that question is the best use of the next research effort.

This distinction matters because research resources are scarce. Funding, researcher time, participants, infrastructure, data access, and institutional capacity devoted to one question cannot simultaneously be devoted to another.

Priority setting therefore requires comparison. The question is not merely “Would answering this be useful?” but “Would answering this be more valuable than the realistic alternatives?”

This shifts attention from the existence of a gap to the value of knowing the answer to the research question.

Begin by defining what could change if the question were answered

For each candidate research question, ask what becomes possible if the uncertainty is reduced.

In applied research, the answer may concern a decision: whether to adopt an intervention, choose one policy over another, allocate resources differently, change an educational practice, or target an intervention to a particular population.

For other research, the contribution may be scientific rather than immediately decision-oriented. A study might resolve a theoretical disagreement, improve measurement, establish whether a phenomenon exists, create a reusable method, or provide foundational evidence needed for subsequent research.

The important point is to make the expected contribution explicit. “Nobody has studied this yet” describes the literature. It does not explain why the answer deserves priority.

For decision-oriented research, identify the decision before ranking the questions

Value-of-information analysis begins from a defined decision problem. Current evidence supports some choice among available alternatives, but uncertainty means that this choice may turn out to be suboptimal. Further research can have value when reducing uncertainty allows better decisions.

That framing changes how research questions are compared. Instead of asking which parameter is least certain, ask which uncertainty contributes most to the expected consequences of making the wrong decision.

This is also why the question with the greatest uncertainty is not automatically the question with the greatest consequences.

Not every uncertainty matters equally to the decision

Suppose a decision model contains uncertain estimates of effectiveness, costs, long-term persistence, uptake, and adverse outcomes. Researchers may know much less about uptake than effectiveness. Yet if plausible uptake values barely affect which action is preferred, improving that estimate may have little decision value.

Meanwhile, a relatively narrow uncertainty around long-term effectiveness could be crucial if modest changes reverse the preferred decision.

Research prioritization should therefore identify which uncertainty is actually worth reducing rather than treating every gap as equivalent.

Consequences matter alongside the probability of being wrong

A question can be valuable because current uncertainty creates a substantial chance of making the wrong decision. But probability alone is not enough.

Suppose Question A concerns a decision with a 30% probability that the currently preferred option is not actually best, but the alternatives have almost identical outcomes. Question B concerns a decision with only a 5% probability of error, but choosing incorrectly would produce substantial harm or waste.

Question A is more uncertain in one sense. Question B may nevertheless be more valuable to resolve because the expected consequences of error are larger.

The comparison therefore needs to incorporate both uncertainty and what is at stake.

EVPI asks how much eliminating all decision uncertainty could be worth

The expected value of perfect information (EVPI) estimates the expected improvement in outcomes if all uncertainty represented in a decision problem could be resolved before choosing an action. It therefore provides an upper bound on the value of eliminating that uncertainty.

If EVPI is negligible, there may be little decision value available from further research within the specified model. If it is substantial, the next task is to determine which uncertainties account for that value and whether they can realistically be reduced. Value-of-information methods explicitly support this progression from overall decision uncertainty toward research prioritization.

EVPPI helps identify which uncertainty has the greatest potential value

The expected value of partial perfect information (EVPPI) estimates the value of completely resolving uncertainty in a particular parameter or group of parameters while uncertainty elsewhere remains.

EVPPI can therefore help distinguish a parameter that is merely uncertain from one whose uncertainty materially affects the decision. A parameter with a wide distribution may have low EVPPI if changing its value rarely changes the preferred action. A less uncertain parameter may have high EVPPI when it strongly influences decision outcomes.

This is an important step toward identifying candidate research priorities, but it does not yet tell you which actual study should be conducted.

The best theoretical target may not be the best feasible study

EVPPI assumes that the selected uncertainty can be resolved perfectly. Real research cannot usually do that.

A high-value uncertainty may require decades of follow-up, an infeasibly large sample, an unethical experiment, or data that cannot realistically be obtained. Another uncertainty with lower theoretical value might be much easier to reduce through a well-designed study.

The distinction between valuable uncertainty and valuable research is crucial. Research prioritization must consider what a feasible study can actually learn.

EVSI evaluates the information expected from a particular study

The expected value of sample information (EVSI) estimates the expected improvement in decisions from the information that could be generated by a particular proposed study design and sample size.

EVSI therefore moves the comparison from “Which uncertainty would be valuable to eliminate?” to “How valuable would the information from this realistic study be?”

Two studies aimed at the same uncertainty can have different EVSI. A larger study, better measurement strategy, longer follow-up, or more relevant population may reduce uncertainty more effectively. Conversely, additional data can have little value when the study addresses a parameter that does not drive the decision.

Research cost determines whether valuable information is worth obtaining

A study with substantial expected information value may still be a poor research investment if obtaining that information costs even more.

The expected net benefit of sampling (ENBS) compares the expected value of the information generated by a proposed study with its expected research costs. This provides a basis for comparing study designs rather than assuming that the study producing the most information should automatically be preferred.

Formal VOI guidance uses EVPI, EVPPI, EVSI, and ENBS for related but distinct research-prioritization questions. EVPI addresses the total value of eliminating uncertainty, EVPPI identifies the value associated with particular uncertainties, EVSI evaluates proposed study information, and ENBS incorporates research cost.

The number of people who can benefit can change the ranking

The value of an answer often depends on how many future decisions can use it. A tiny expected improvement per person can become substantial when evidence informs decisions affecting a large population over many years.

Conversely, a question involving severe consequences for a very small number of future decisions may have lower total decision value than its individual-level importance initially suggests.

Population-level value-of-information analysis therefore considers the number of people expected to benefit from improved evidence and the period during which the information remains relevant.

This also means that timing matters. Research completed after most relevant decisions have already occurred cannot deliver the same population value as evidence available earlier.

Ask whether the answer will arrive in time to matter

A research question can be important, answerable, and still be a poor immediate priority if the study will take so long that the relevant decision will already have been made or the technology, population, or policy context will have changed.

Research timing therefore belongs in prioritization. A somewhat less valuable question that can be answered quickly enough to improve thousands of imminent decisions may deserve priority over a theoretically more valuable question whose answer arrives too late.

This is closely related to deciding when it is preferable to act with imperfect evidence rather than wait for more research.

Research priority also depends on whether the evidence will be used

Information has little practical effect if it never reaches or influences the people making the relevant decisions. Uptake, implementation, dissemination, institutional authority, and policy constraints can therefore affect the realized value of research.

A study might resolve an important uncertainty yet produce little change if the decision-maker cannot act on the findings. Conversely, research embedded in an active decision process may have unusually high practical value because the route from evidence to action is clear.

This does not mean researchers should study only questions with guaranteed implementation. It does mean that the plausible pathway from evidence to benefit belongs in a serious assessment of research priority.

Priority setting should compare questions on a common basis where possible

Comparing candidate studies becomes easier when each is evaluated through the same questions: What uncertainty does it address? What could change? Who benefits? How much can the study reduce the uncertainty? What does it cost? How long will it take?

This is more defensible than allowing one question to be promoted because it is novel, another because a stakeholder finds it interesting, and a third because its confidence interval happens to be wide.

Formal quantification is not always possible, particularly outside well-specified decision models. A structured qualitative comparison can still make assumptions visible and expose why one question is being prioritized over another.

Stakeholder priorities matter, but they do not eliminate trade-offs

Different stakeholders may value outcomes differently. Researchers, participants, communities, practitioners, policymakers, funders, and institutions may disagree about which uncertainties matter most.

Priority setting should therefore consider whose outcomes and decisions are represented. NICE's research-prioritization process, for example, explicitly distinguishes uncertainties that are merely interesting from those likely to affect recommendations and uses stakeholder-informed processes to identify research priorities.

Stakeholder involvement does not remove the need to compare value, feasibility, and opportunity cost. It helps determine which outcomes and uncertainties deserve to be represented in that comparison.

Not every valuable question has an immediate decision attached to it

Value-of-information analysis is particularly useful when research is intended to inform a clearly defined decision under uncertainty. It should not become the universal definition of worthwhile science.

Basic, exploratory, theoretical, and methodological research may generate discoveries whose eventual uses cannot be forecast credibly. A foundational measurement tool, theoretical insight, or new method can enable many later studies without changing an immediate policy or practice decision.

For such questions, researchers still need to compare potential contribution, tractability, scientific importance, opportunity cost, and alternatives. The form of value is broader, however, and should be stated honestly rather than forced into an artificial immediate decision model.

Four unanswered questions compete for one research grant

The priority could change as evidence, costs, methods, or decisions change. If a large administrative dataset later makes subgroup effects inexpensive to estimate, Question D could become the better research investment. Research priorities are conditional on the information and opportunities available at the time.

Common mistakes when deciding what to research next

Compare candidate questions by the difference their answers could make

When choosing what to study next, create a shortlist of genuine candidate questions rather than evaluating your preferred topic in isolation. For each candidate, specify what is uncertain, what answering it could change, and what study would be needed to reduce the uncertainty.

Then compare the candidates on consequences, information gain, feasibility, cost, timing, and the number of future decisions or scientific activities that could benefit.

This approach also clarifies when not to conduct another study. A question can be interesting yet offer so little incremental benefit that the resources would produce greater value elsewhere. In that case, conducting research simply because the question remains unanswered can have negative net value.

The aim is not to identify the objectively “best” research question for all purposes. It is to make the reasoning behind the next research investment explicit enough that competing questions can be compared rather than selected by habit, visibility, or novelty alone.

Before deciding what research question to answer next

Questions about choosing the most valuable research question

The best next question is the one whose answer creates the greatest attainable value

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