One of the most exciting events in researchers' lives happens when students or working clinicians come to us with ideas for a research project. Sometimes these ideas involve basic research and emerge during the process of undergraduate or graduate teaching. Sometimes they are applied questions and result from intuitive clinical observations by a practicing clinician.
It is imperative for the continued cutting-edge assessment and treatment of our clients that new researchers ask new questions and develop the skills to translate these into viable research studies. However, the formulation of a good research question is more difficult than it first appears.
It is almost a given that, early in their research careers, people ask the "wrong" kinds of questions. This mistake occurs for some very good reasons. Often people are very excited and creative when asking these early questions; in the long run, such insight and enthusiasm leads to new and critical questions in the field. However, some tips can be learned to translate unbridled enthusiasm into a question that can be answered and can contribute in substantive ways to the knowledge base and clinical approaches in the field.
What should a good research question include? In many ways, it is easiest to answer this question through examples of common mistakes:
- Some questions are too vague, and/or too broad: Does background noise affect children when they learn?
- Some may be too narrow for general research (although they may be interesting as single-subject studies intended to influence local changes): Is it difficult for Child A to hear final /s/ with the windows open in classroom B of school C?
- Some are diffuse and not well-focused: I'd like to study speech production characteristics of people with cleft palate, and while testing them, I'll also test their perception of nasality in others' speech.
- Some questions aren't easily measurable as stated: Are children distractible in noise?
- Others may be measurable but not valuable to test. A common pitfall is to propose testing something just because "it's never been done." We may have learned a great deal from past research about understanding CID sentences in varying kinds of noise, but no one has studied perception of BKB sentences in all those noises. That isn't sufficient motivation to proceed with a study of BKB sentence understanding in noise.
Still others are driven by the strong desire to prove something is right or wrong. (I already believe therapy method X is the best for adults with aphasia, and I'm going to prove it!) Good research questions can be answered in the affirmative or negative and still be worth studying.
Sometimes the measurement tools chosen answer the wrong question (or a different question.) For example, the researcher may incorporate actors and recipients such as a hippopotamus and a chimpanzee in the study of young children's ability to produce passives. Perhaps this inadvertently becomes a measure of vocabulary knowledge rather than the syntactic structure being tested.
Evolution of Research Questions
Research questions do evolve as projects get underway. That's natural. And it's natural to occasionally lose sight of the original question as we delve into the project. It's important always to return to the original question to make sure we're still on track to measure what is appropriate to answer that question.
So, what is an example of a good question? What components need to be considered, and how does such a question evolve? To address this, we will provide two examples of the evolution of questions. These examples were obtained from our experiences with clinicians and student researchers who had very important questions they wanted to learn to answer.
Example 1. Recently a clinician working in schools with bilingual children approached one of us with a concern that his English-language-learning (ELL) children may be at a distinct disadvantage in the large, noisy urban classrooms that he served.
I thought this was a great question, that could be narrowed and tested in a useful way, and that the results might have implications for other children and clinicians. We brainstormed ideas, read and discussed the relevant literature, observed in the classrooms, talked with the teachers, and eventually narrowed the focus of the study to word (picture) recognition by groups of monolingual English-speaking and ELL second grade children in two levels of background noise.
We chose simple stimuli that would be appropriate for all the children, incorporated picture pointing tasks that all could do, and tested the children in the classrooms but with recorded noise levels that we could control.
We determined that the ELL children showed performance equal to that of monolingual children in quiet, but not in noise. That finding helped us answer the original question in the affirmative: Yes, ELL children are at a disadvantage in noisy classrooms, even when the stimuli are familiar and easily identified in quiet.
Example 2. A doctoral student entered the lab after practicing clinically for a few years. She had a broad notion of what she wanted to study in graduate school. She was interested in cross-domain (especially motor) effects on phonological acquisition in children with speech and language disorders.
Over the course of her doctoral career, this question became increasingly focused and specified, yet continued to address the very important theme that had inspired her to return to graduate school. By the time she worked on her dissertation, she was able to ask: Do phonotactic frequency or neighborhood density effects influence motor or phonological aspects of word production in children with specific language impairment?
This contained the elements of a good question. Most critically, it was theoretically and clinically important. She carefully reviewed the literature to develop a stimulus set and an experimental task that was valid and replicable. She included a well-defined clinical population so that her results could be generalized to other groups of children.
In the end, she found out that neighborhood factors influence phonological aspects of speech production and frequency factors influence motor aspects. These results have theoretical implications and also contribute to how the clinician may think about stimulus selection and learning in the course of intervention. This trajectory from a broad and general to a well-specified research question is an illustration of the exciting process of becoming a mature researcher. It is indeed a rich and rewarding journey.
Diving Into Research
So what does this mean if you're a new researcher considering diving into this exciting process? We recommend paying attention to something that intrigues you in class or clinic. Consider possible questions that may be worth exploring. Read the literature on the topic to determine areas that remain in question. Brainstorm ideas with a seasoned researcher to come up with a focused, measurable question whose answer may contribute to our understanding of the science.
A good research question will ultimately help shape your choice of methods, stimuli, participants, and analysis. When all goes well, the research results in a clear answer to a clearly stated question, with implications for our science and clinical practice. Nothing is more rewarding.
Next in the research series: Experimental Bias and Blinding.