How do I turn a research topic into a research question?

Topics are comfortable because they cannot be wrong. "Teacher retention" commits you to nothing, which is why it survives so long in proposals. The move to a question is the move to something that could turn out false, and the discomfort people feel at this stage is exactly the discomfort of committing.

The four additions do most of the work. Start with the relationship: what connects to what, or what varies with what, or what is the character of what. Then the population, since "teachers" is not a population but "teachers in their first five years in state secondary schools" is. Then the context, which is where and when. Then the outcome, which is the thing you will actually observe.

A published stepwise version of this works the same way. Ratan and colleagues start from "hormone levels among hypospadias", read what is already established about testosterone, and write down what remains unknown about the other reproductive hormones. Only then does the topic become a question about how hormone levels differ between children with isolated hypospadias and a normal population (Ratan et al., 2019, p. 18). The written information gap is the hinge. Without it you are guessing at what your relationship, population, context, and outcome should be.

That means the literature review is not background you bolt on after choosing the question. It is the instrument that tells you whether the topic contains a researchable problem at all. Pautasso is specific about the labour involved: search with several different keyword sets, use more than one database such as Google Scholar, JSTOR, Medline, Scopus, and Web of Science, and follow forward citations to see who has used the papers and book chapters you found (Pautasso, 2013, pp. 1-2). Note that this is practical advice drawn from roughly 25 reviews he completed as a doctoral student and postdoc, not a comparative study of methods, so treat it as a working procedure rather than a tested one.

Run the result past a colleague and watch for a specific failure. If they respond by telling you what they think about the topic, you still have a topic. If they respond by guessing what the answer might be, you have a question, because a question is a thing people can have expectations about.

Expect to produce six or seven versions. The first is too broad, the second overcorrects into something trivial, and the usable one usually appears around the fourth. This is normal and fast, and it is much cheaper than discovering the problem after data collection.

Score the surviving version against criteria instead of instinct. Ratan and colleagues use the acronym FINERMAPS: feasible, interesting, novel, ethical, relevant, manageable, appropriate, potentially valuable and publishable, and systematic. They add that the question must be more complex than a yes-or-no answer, measurable through data that could support or contradict it, and neither too broad nor too narrow (Ratan et al., 2019, pp. 15-16). Their reading of novelty is looser than most students assume. Confirming or refuting an established finding counts, and so does examining a new aspect of a problem others have already worked on (Ratan et al., 2019, p. 17).

How narrow does a research question need to be?

Narrow enough that you can name the evidence that would answer it. If you cannot describe the dataset, sample, or corpus that settles the question, it is still too broad. That test is more reliable than word count, and it catches questions that sound specific but are not.

Apply it literally. Say out loud what you would need: how many participants, what documents, what measurements, over what period. If that description is vague, the vagueness is in the question rather than in your planning.

The same test catches the opposite problem. If the evidence you name is trivially easy to gather and the answer is obvious in advance, the question is too narrow to be worth three years.

Feasibility belongs in this test too, and it covers more than sample size. Ratan and colleagues list the subjects, method, data access, equipment, documents, statistics, time, and funds that all have to be available before a question counts as answerable, and they warn that a question can look feasible on paper and turn impractical once fieldwork starts. Their remedy is to report the problem honestly, talk to your supervisor or experienced colleagues, and hold a contingency plan (Ratan et al., 2019, p. 16). They also recommend one clear key question with several subcomponents rather than a flat list of equals (Ratan et al., 2019, p. 17). Pautasso pushes in the other direction and asks you to keep the narrow question tied to a wider concern, since a review that is too focused stops being interesting to anyone outside it (Pautasso, 2013, p. 3). Both constraints hold at once. Narrow enough to finish, connected clearly enough that someone else cares about the answer.

What is the difference between a research question and a research aim?

An aim states what you will do, a question states what you will find out. "To explore the role of informal mentoring" is an aim and cannot be answered, only performed. "Does informal mentoring predict retention independently of formal programmes" is a question with a possible answer of no.

Most theses need both, and confusion arises because supervisors and templates use the words loosely. Write the aims as a short list of activities and the questions as sentences ending in question marks, and keep them visually separate on the page. A reader should never have to work out which is which.

The diagnostic word is "explore". It is not forbidden, and a genuinely exploratory study is a real design, but it is also where unanswerable questions hide. If "explore" is doing the analytical work in your sentence, ask what you would conclude at the end and put that in the question instead.