03 · What You Need to Know
The Criteria That Help Distinguish a Promising Idea From a Pursuable Study
Potential Contribution: What Would Change If You Answered the Question?
Begin with the contribution the study could make. A research project consumes time, expertise, participant effort in some fields, institutional resources, and often funding. There should be a defensible reason to conduct it.
Contribution can take different forms. A study might address an important unresolved question, challenge an established explanation, extend evidence to an inadequately studied context, improve measurement or methodology, resolve conflicting findings, or produce knowledge useful to practice or policy.
This does not require every project to promise a dramatic breakthrough. NIH's current peer-review framework asks reviewers to assess whether proposed research addresses an important knowledge gap, solves a critical problem, or creates a valuable conceptual or technical advance. It also explicitly recognizes that research can be critically important without relying on highly novel concepts or approaches.
A practical question is: If this study is completed well, what credible contribution could it make?
Importance and Relevance: Does the Question Deserve Attention?
Contribution and importance overlap, but they are not identical. Contribution concerns what new knowledge the study may produce. Importance concerns why producing that knowledge matters.
Relevance may be scientific, theoretical, methodological, practical, clinical, educational, social, or policy-related depending on the field. FINER explicitly includes relevance to scientific knowledge and, in its clinical formulation, relevance to clinical and health policy and future research.
Importance should nevertheless be argued rather than assumed. A topic affecting many people may contain a narrowly consequential research question, while a question concerning a relatively small population may address a serious unresolved problem.
Feasibility: Can You Conduct the Study Properly?
Feasibility asks whether the idea can become a rigorous study under realistic conditions. In FINER, this includes considerations such as adequate participants, technical expertise, affordability in time and money, and manageable scope.
NIH similarly evaluates whether proposed studies can be done well within the proposed timeframe and whether the approach is sound and achievable. Depending on the study, feasibility may involve recruitment, data access, equipment, software, laboratory capacity, permissions, funding, collaborators, or time.
Feasibility should not be confused with ease. A difficult project may still be highly feasible if the necessary capabilities are available. An apparently simple project may become infeasible if its essential data cannot be obtained.
This criterion becomes particularly important when a more important question is substantially harder to execute.
Methodological Answerability: Can the Proposed Evidence Actually Answer the Question?
An idea may be interesting and feasible in a logistical sense yet poorly matched to the evidence or design available.
A well-defined research question helps determine study design, population, data collection, and analysis. Research-question guidance has long emphasized that poorly formulated questions can lead to inappropriate designs and results that do not meaningfully address the intended problem.
Ask whether there is a defensible empirical or analytical path from the research question to an answer. If the available method can address only a weaker or different question, either refine the idea or acknowledge what the study can actually establish.
Ethical Acceptability: Should the Study Be Conducted in the Proposed Form?
Ethics is not merely another attractive characteristic. FINER treats ethical acceptability as a basic characteristic of a good research question, and research involving humans, animals, sensitive data, or consequential interventions may require additional formal safeguards and approvals.
This is one reason an ethical problem should not simply receive a low score and then be compensated for by high scores elsewhere.
Watch Out
Do not use an overall score to make a fundamentally unacceptable study appear acceptable. Some criteria establish whether an idea can remain under consideration at all.
Originality: What Is New About the Proposed Contribution?
Originality matters, but it requires careful interpretation. FINER defines novelty broadly enough to include research that confirms, refutes, or extends previous findings. NIH similarly notes that a project without highly novel concepts or approaches can still be critically important.
Accordingly, originality should not be reduced to “Has nobody ever studied this before?” A study can make an original contribution through a new question, population, context, theoretical interpretation, dataset, method, comparison, or synthesis, provided that the difference is consequential rather than cosmetic.
When two ideas differ sharply here, examine what originality and practical relevance actually contribute to each option rather than automatically privileging one.
Access to Suitable Evidence: What Will You Actually Be Able to Observe?
Data availability deserves explicit consideration because your conclusions are constrained by the evidence you can obtain.
For primary research, this might concern access to participants, sites, records, instruments, archives, samples, or observations. For secondary research, it may involve dataset coverage, variable quality, missingness, documentation, access restrictions, or whether the data correspond to the constructs in the research question.
Better data should not automatically defeat a more important question. But differences in data access can change which study is scientifically executable, not merely which one is convenient.
Expertise and Resources: Can You or Your Team Do the Work Well?
A study can be feasible in principle but not feasible for the current research team. Some projects require statistical, qualitative, computational, laboratory, clinical, linguistic, technical, or disciplinary expertise that is not readily substitutable.
NIH explicitly considers whether investigators possess appropriate background, training, and expertise and whether institutional resources are suitable for successful execution. This is a useful reminder that research ideas are pursued by actual teams in actual environments.
A gap in expertise does not necessarily eliminate an idea. It may instead identify the collaborator, training, infrastructure, or methodological consultation required before proceeding.
Uncertainty and Research Risk: How Fragile Is the Path to a Useful Result?
Research necessarily involves uncertainty. The relevant question is what kind of uncertainty an idea carries and whether its potential contribution justifies it.
A project may depend on uncertain recruitment, an untested method, difficult measurement, a speculative mechanism, or access that has not yet been secured. These uncertainties do not all have the same consequences.
NIH's current feasibility guidance explicitly asks reviewers, where feasibility is less certain, to consider whether that uncertainty is balanced by the potential for major advances. That is a useful principle beyond grant review: risk should be interpreted alongside potential value rather than treated as automatically good or bad.
This becomes especially relevant when deciding whether a riskier research idea is worth pursuing.
Personal Interest and Intellectual Fit: Will You Want to Stay With the Question?
FINER includes whether the answer interests the investigator, peers, and community. Personal interest is therefore not frivolous. Research often requires prolonged attention, repeated problem-solving, and tolerance for frustrating stretches in which the data stubbornly decline to behave like the methods textbook promised.
Still, personal enthusiasm does not rescue a weak question. It is more defensible as one consideration among scientifically viable alternatives, particularly when two ideas are otherwise closely matched scientifically.
Strategic Fit: Does the Idea Make Sense in Your Present Research Context?
Some considerations are contextual rather than intrinsic to the research question. An idea may connect with your developing expertise, available collaborators, an existing dataset, a larger program of work, or an opportunity to build capabilities needed for subsequent studies.
This criterion should be used carefully. Strategic convenience should not replace scientific justification. But when several ideas are worthwhile, it can reasonably affect which one you pursue first.
Publication or Funding Potential: Usually Secondary, Sometimes Relevant
Researchers operate within institutions, careers, funding systems, and publication environments, so pretending these considerations never matter would be unrealistic. The problem arises when they become substitutes for scientific merit.
Publication potential may reasonably influence a genuinely close choice, but a fashionable or easily publishable topic is not automatically a stronger research question. Similarly, funding prospects may affect whether a resource-intensive study can actually happen, but fundability and scientific importance are not synonymous.
These factors are usually better treated as contextual or tie-breaking considerations after the scientific case has been established.
You Do Not Need Every Criterion for Every Decision
A useful framework should discriminate among your alternatives. If all three ideas require essentially the same resources, resource availability may not help distinguish them. If none involves meaningful differences in data access, that criterion may deserve little attention in the comparison.
Conversely, a criterion omitted from a generic framework may be decisive in a particular field. A longitudinal study may depend heavily on participant retention. An archival project may depend on access permission. A computational project may require resources that make scale a central feasibility issue.
The criteria should serve the decision, not become a form that must be completed for its own sake.
