The research question is the uncertainty that the investigator wants to resolve by performing his/her study. There is no shortage of good research questions, and even as we succeed in answering some questions, we remain surrounded by others. Clinical trials, for example, established that treatments that block the synthesis of estradiol (aromatase inhibitors) reduce the risk of breast cancer in women who have had early stage cancer. But this led to new questions: How long should treatment be continued; does this treatment prevent breast cancer in patients with BRCA 1 and BRCA 2 mutations; and what is the best way to prevent the osteoporosis that is an adverse effect of these drugs? Beyond that are primary prevention questions: Are these treatments effective and safe for preventing breast cancer in healthy women?

Origins of A Research Question

For an established investigator the best research questions usually emerge from the findings and problems she has observed in her own prior studies and in those of other workers in the field. A new investigator has not yet developed this base of experience. Although a fresh perspective is sometimes useful by allowing a creative person to conceive new approaches to old problems, lack of experience is largely an impediment.

A good way to begin is to clarify the difference between a research question and a research interest. Consider this research question:

  • Dose participation in group counseling sessions reduce the likelihood of domestic violence among women who have recently immigrated from Central America?

This might be asked by someone whose research interest involves the efficacy of group counseling, or the prevention of domestic violence, or improving health in recent immigrants. The distinction between research questions and research interests matters because it may turn out that the specific research question cannot be transformed into a viable study plan, but the investigator can still address research interest by asking a different question.

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Of course, it’s impossible to formulate a research question if you are not even sure about your research interest (beyond knowing that you’re supposed to have one). If you find yourself in this boat, you’re not alone: Many new investigators have not yet discovered a topic that interests them and is susceptible to a study plan they can design. You can begin by considering what sorts of research studies have piqued your interest when you’ve seen them in a journal. Or perhaps you were bothered by a specific patient whose treatment seemed inadequate or inappropriate: What could have been done differently that might have improved her outcome? Or one of your attending physicians told you that hypokalemia always caused profound thirst, and another said the opposite, just as dogmatically.

Mastering the Literature

It is important to master the published literature in an area of study: Scholarship is a necessary precursor to good research. A new investigator should conduct a thorough search of published literature in the areas pertinent to the research question and critically read important original papers. Carrying out a systematic review is a great next step for developing and establishing expertise in a research area, and the underlying literature review can serve as background for grant proposals and research reports. Recent advances may be known to active investigators in a particular field long before they are published. Thus, mastery of a subject entails participating in meetings and building relationships with experts in the field.

Being Alert to New Ideas and Techniques

In addition to the medical literature as a source of ideas for research questions, it is helpful to attend conferences in which new work is presented. At least as important as the formal presentations are the opportunities for informal conversations with other scientists at posters and during the breaks. A new investigator who overcomes her shyness and engages a speaker at the coffee break may find the experience richly rewarding, and occasionally she will have a new senior colleague. Even better, for a speaker known in advance to be especially relevant, it may be worthwhile to look up her recent publications and contact her in advance to arrange a meeting during the conference.

A skeptical attitude about prevailing beliefs can stimulate good research questions. For example, it was widely believed that lacerations which extend through the dermis required sutures to assure rapid healing and a satisfactory cosmetic outcome. However, Quinn et al. noted personal experience and case series evidence that wounds of moderate size repair themselves regardless of whether wound edges are approximated. They carried out a randomized trial in which all patients with hand lacerations less than 2 cm in length received tap water irrigation and a 48-hour antibiotic dressing. One group was randomly assigned to have their wounds sutured, and the other group did not receive sutures. The suture group had a more painful and time-consuming treatment in the emergency room, but blinded assessment revealed similar time to healing and similar cosmetic results. This has now become a standard approach used in clinical practice.

The application of new technologies often generates new insights and questions about familiar clinical problems, which in turn can generate new paradigms. Advances in imaging and in molecular and genetic technologies, for example, have spawned translational research studies that have led to new treatments and tests that have changed clinical medicine. Similarly, taking a new concept, technology, or finding from one field and applying it to a problem in a different field can lead to good research questions. Low bone density, for example, is a risk factor for fractures. Investigators applied this technology to other outcomes and found that women with low bone density have higher rates of cognitive decline, stimulating research for factors, such as low endogenous levels of estrogen, that could lead to loss of both bone and memory.

Keeping the Imagination Roaming

Careful observation of patients has led to many descriptive studies and is fruitful source of research questions. Teaching is also an excellent source of inspiration; ideas for studies often occur while preparing presentations or during discussions with inquisitive students. Because there is usually not enough time to develop these ideas on the spot, it is useful to keep them in a computer file or notebook for future reference.

There is a major role for creativity in the process of conceiving research questions, imagining new methods to address old questions, and playing with ideas. Some creative ideas come to mind during informal conversations with colleagues over lunch; others arise from discussing recent research or your own ideas in small groups. Many inspirations are solo affairs that strike while preparing a lecture, showering, perusing the Internet, or just sitting and thinking. Fear of criticism or seeming unusual can prematurely quash new ideas. The trick is to put an unresolved problem clearly in view and allow the mind to run freely around it. There is also a need for tenacity, returning to a troublesome problem repeatedly until a resolution is reached.

Choosing and Working with a Mentor

Nothing substitutes for experience in guiding the many judgements involved in conceiving a research question and fleshing out a study plan. Therefore an essential strategy for a new investigator is to apprentice herself to an experienced mentor who has the time and interest to work with her regularly.

A good mentor will be available for regular meetings and informal discussions, encourage creative ideas, provide wisdom that comes from experience, help ensure protected time for research, open doors to networking and funding opportunities, encourage the development of independent work, and put the new investigator’s name first on grants and publications whenever appropriate. Sometimes it is desirable to have more than one mentor, representing different disciplines. Good relationships of this sort can also lead to tangible resources that are needed – office space, access to clinical populations, data sets and specimen banks, specialized laboratories, financial resources, and a research team.

Characteristics of A Good Research Question

  • Feasible

It is best to know the practical limits and problems of studying a question early on, before wasting much time and effort along unworkable lines.

Number of subjects. Many studies do not achieve their intended purposes because they can not enroll enough subjects. A preliminary calculation of the sample size requirements of the study early on can be quite helpful, together with an estimate of the number of subjects likely to be available for the study, the number who would be excluded or refuse to participate, and the number who would be lost to follow up. Even careful planning often produces estimates that are overly optimistic, and the investigator should assume that there are enough eligible and willing subjects. It is sometimes necessary to carry out a pilot survey or chart review to be sure. If the number of subjects appears insufficient, the investigator can consider several strategies: expanding the inclusion criteria, eliminating unnecessary exclusion criteria, lengthening the time frame for enrolling subjects, acquiring additional sources of subjects, developing more precise measurement approaches, inviting colleagues to join in a multi center study, and using a different study design.

Technical expertise. The investigators must have skills, equipment, and experience needed for designing the study, recruiting the subjects, measuring the variables, and managing and analyzing the data. Consultants can help to shore up technical aspects that are unfamiliar to the investigators, but for major areas of the study it is better to have an experienced colleague steadily involved as a coinvestigator; for example, it is wise to include a statistician as a member of the research team from the beginning of the planning process. It is best to use familiar and established approaches, because the process of developing new methods and skills is time-consuming and uncertain. When a new approach is needed, such as measurement of a new biomarker, expertise in how to accomplish the innovation should be sought.

Cost in time and money. It is important to estimate the costs of each component of the project, bearing in mind that the time and money needed will generally exceed the amounts projected at the outset. If the projected costs exceed the available funds, the only options are to consider a less expensive design or to develop additional sources of funding. Early recognition of a study that is too expensive or time-consuming can lead to modification or abandonment of the plan before expending a great deal of effort.

Scope. Problems often arise when an investigator attempts to accomplish too much, marking many measurements at repeated contacts with a large group of subjects in an effort to answer too many research questions. The solution is to narrow the scope of the study and focus only on the most important goals. Many scientists find it difficult to give up the opportunity to answer interesting side questions, but the reward may be a better answer to the main question at hand.

Fundability. Few investigators have the personal or institutional resources to fund their own research projects, particularly if subjects need to be enrolled and followed, or expensive measurements must be made. The most elegantly designed research proposal will not be feasible if no one will pay for it.

  • Interesting

An investigator may have many motivations for pursuing a particular research question: because it will provide financial support, because it is a logical or important next step in building a career, or because getting at the truth of the matter is interesting. We like this last reason; it is one that grows as it is exercised and that provides the intensity of effort needed for overcoming the many hurdles and frustrations of the research process. However, it is wise to confirm that you are not the only one who finds a question interesting. Speak with mentors, outside experts, and representatives of potential funders such as NIH project officers before devoting substantial energy to develop a research plan or grant proposal that peers and funding agencies may consider dull.

  • Novel
Good clinical research contributes new information. A study that merely reiterates what is already established is not worth the effort and cost and is unlikely to receive funding. The novelty of a proposed study can be determined by thoroughly reviewing the literature, consulting with experts who are familiar with unpublished ongoing research, and searching for abstracts of projects in your area of interest that have been funded using the NIH Research Portfolio Online Reporting Tools (RePORT) website. Reviews of studies submitted to NIH give considerable weight to whether a proposed study is innovative such that a successful result could shift paradigms of research or clinical practice through the use of new concepts, methods, or interventions. Although novelty is an important criterion, a research question need not be totally original – it can be worthwhile to ask whether a previous observation can be replicated, whether the findings in one population also apply to others, or whether a new measurement method can clarify the relationship between known risk factors and a disease. A confirmatory study is particularly useful if it avoids the weaknesses of previous studies or if the result to be confirmed was unexpected.
  • Ethical
A good research question must be ethical. If the study poses unacceptable physical risks or invasion of privacy, the investigator must seek other ways to answer the question. If there is uncertainty about whether the study is ethical, it is helpful to discuss it at an early stage with a representative of the institutional review board (IRB).
  • Relevant
A good way to decide about relevance is to imagine the various outcomes that are likely to occur and consider how each possibility might advance scientific knowledge, influence practice guidelines and health policy, or guide further research. NIH reviewers emphasize the significance of a proposed study: the importance of the problem, how the project will improve scientific knowledge, and how the result will change concepts, methods, or clinical services.
Developing the Research Question and Study Plan
It helps a great deal to write down the research question and a brief (one-page) outline of the study plan at an early stage (detail here This requires some self-discipline, but it forces investigator to clarify her ideas about the plan and to discover specific problems that need attention. The outline also provides a basis for specific suggestions from colleagues.