From Idea to Research Question

Every research project starts as a vague interest and has to become one clear question you can answer with data in a few months. This guide walks you through that change, step by step, until you have a one-page research proposal your mentor can review. You don't need any background beyond curiosity and a willingness to rewrite your question several times.

What you'll be able to do when you finish

• Tell a strong research question from a weak one, and explain why, using the FINER criteria and PICO.
• Name the type of question you are asking (descriptive, comparative, relational, causal, predictive, or engineering) and the kind of study each type needs.
• Turn a broad interest into a narrow, measurable question with operational definitions for every variable.
• Write a testable hypothesis, or engineering goals with criteria when a hypothesis doesn't fit.
• Choose a study design, spot confounding variables, and plan controls, randomization, and repeated trials.
• Check that data exists and that you are allowed to use it before you commit.
• Build a realistic 12 to 16 week timeline with milestones and backup plans.
• Know which projects need review and approval before you start, and work well with a mentor.
• Write a complete one-page research proposal.

How each chapter is built

Each chapter starts with the idea in plain words, then shows it with worked examples from several fields: biology, environmental science, computer science, psychology, and physics or engineering. Most chapters include a table you can come back to as a reference, and a few include sample writing you can model. Every chapter except this one and the glossary ends with a short Check yourself list. If you can answer those questions without looking back, move on.

Keep a running document called your question log. Every time a chapter asks you to try something (brainstorm topics, rewrite a question, define a variable), do it in that document. By the last chapter, the log will hold almost everything you need for your proposal.

A suggested pace

Some students move faster and some need five or six weeks, especially if the first idea doesn't survive the feasibility check in Chapter 8. That's normal. A question that dies in week 3 costs you far less than one that dies in week 10.

This guide is the Ask stage of Vector Research. If you haven't yet learned how to find and read papers, read "Finding and Reading Research Papers" alongside Chapters 4 and 5. When you reach the analysis plan, "Statistics for Research" covers the tests in depth.

A research question is a single, precise question that your project is designed to answer. Everything else in a project (the data you collect, the methods you choose, the graphs on your poster) exists to answer it, so a fuzzy question produces a fuzzy project.

Five properties of a strong question

Researchers describe good questions in different ways, but most descriptions share five properties. Use these as a checklist every time you write or revise a question.

Take a common starting point: "Does social media affect teenagers?" It fails almost every test. "Affect" could mean mood, sleep, grades, or friendships. "Social media" could mean any app, used in any way. There's no population, no time frame, and no measurement. Compare it with this version:

"Among 9th to 12th graders at one high school who complete an anonymous survey, is reporting 3 or more hours per school day on social media associated with reporting fewer than 8 hours of sleep on school nights?"

Now you can picture the answer. It would be a table comparing two groups, with the percentage of each group sleeping fewer than 8 hours. That ability to picture the final table or graph is the fastest test of whether a question is answerable. (A survey like this involves human participants, so it needs approval before you collect anything; see Chapter 10.)

How original is original enough

High school researchers often freeze because they think a question has to be completely new. It doesn't. Professional scientists rarely ask a question nobody has touched. They ask one that extends earlier work in a small, clear way. Your question is original enough if it does at least one of these:

• Tests a known finding in a new population (a different age group, region, species, or soil type).
• Uses a newer or larger dataset than earlier studies had.
• Applies a different method to an old question, such as a machine learning model where earlier work used a simple regression.
• Combines two datasets that nobody has linked before, such as air quality readings and school attendance.
• Replicates an important study to see whether the result holds up.

You can only know where your question sits if you've read the closest published work. That's why reading papers comes before finalizing the question, and why Chapter 4 shows you how to mine papers for ideas.

The FINER criteria

Clinical researchers use a well-known checklist called FINER, described in the textbook Designing Clinical Research by Stephen Hulley, Steven Cummings, and colleagues. It appears in the chapter "Conceiving the research question and developing the study plan," which is Chapter 2 of the fourth edition (2013), written by Cummings, Warren Browner, and Hulley. The fifth edition was published in 2022. FINER says a good question is:

Although FINER came from clinical research, it works for any field. Feasibility is where most student projects fail, so give it the most weight. A brilliant question you cannot answer by your fair date is a worse choice than a modest question you can answer well.

A worked FINER check

Here's a student's first question and an honest FINER check.

First draft: "Can a new drug slow memory loss in people with early Alzheimer's disease?"

Revised: "In public gene expression data from brain tissue in NCBI GEO, which genes differ most in expression between people with and without Alzheimer's disease, and do those genes cluster in known biological pathways?"

The revision keeps the interesting, relevant core and moves it to a form a student can do with public, de-identified data, a laptop, and free software. Feasible and ethical now pass. Novelty depends on which dataset and which pathways, and reading the literature will tell you.

Questions that are too big, too small, or not research

Three kinds of questions show up again and again in early drafts.

• Too big. "What causes cancer?" Whole careers and institutes work on this. Shrink the population, the variable, and the outcome until a few months of work could answer it.
• Too small. "What is the boiling point of water at my house?" You can look it up or measure it in five minutes, and the answer teaches nothing new. Expand it into a pattern: how does boiling point change across a range of altitudes or dissolved salt concentrations, and does it match the theory?
• Not research. "Should schools ban phones?" This is a values question. Data can inform it (does banning phones change test scores?), but data alone can't settle what people should do. Rewrite it into the empirical part you can measure.