Narrowing Your Focus

December 1, 2014

Dr. Laura:

I recently completed my coursework and am moving into the process of writing the proposal. How do I shift my focus from the research pie to just a slice of the pie?

Thank you, Swimming in ideas

Dear Swimming in Ideas,

The doctoral program requires transition from a period of somewhat unrestricted exploration (i.e., the first years of a doctoral program) to a period of sharp focus where ideas are honed and precise planning is undertaken (i.e., actual dissertation research and writing). Learning how to make these shifts is one of the skills you will need to master. And master it you will, I’m sure :-)

To take a big area of interest and distill it to a workable research question, I suggest you first identify some research areas of interest that are in need of further study, that require some resolution.Then evaluate these areas based on your passion for the idea, the idea’s meatiness, its potential to lead to future work, its feasibility when translated into a research study, and its potential to contribute to the field.

Identify a Need (aka Problem) in an Area that Excites You
Consider your broader area of interest and ask yourself these questions:

  • What do I want to know?
  • Why do I want to know it?

This will help you identify facets of your broader area of interest that really excite you. Then go through the literature, if you haven’t already, and identify “problems”: those areas where there are disagreements, gaps in knowledge, needs for analysis, incomplete exploration of the issues, or descriptive statements about an issue but little coherent explanation or interpretation. What are scholars citing as the open questions in your area of interest?

Evaluate and Compare Your Ideas
Once you find some real needs for research that jibe with your interests, you could try classifying them by:

  • Passion: what seems most interesting to you,
  • Substance: how strong is the idea (is there anything to the idea?),
  • Promise of Future work: what has the most conceptual linkages to other things you’re interested in,
  • Feasibility: what can be translated into a research study, and
  • Contribution to the Field: how would it contribute to the field of library and information science–is it also interesting to other researchers and practitioners?

Classifying ideas/needs by what you’re passionate about would hopefully be straightforward at this point, because you will have asked yourself why do I want to know it? Whatever big question you target, I encourage you to find a piece of the pie that you actually want to eat. If you love your topic, it will be easier to devote the time and intensity required for completion of the dissertation. Furthermore, the delight you take in the topic will better sustain you through a long career pursuing a research agenda built on of that topic.

Consider your ideas in terms of how weighty they are. For example, if you want to replicate a study but in a different context or with different subjects, then ask yourself first whether there is a sufficient conceptual rationale for expecting that this new context or population will be any different. If this study has been done with students, firefighters, and nurses, do you have sufficient evidence theoretically to expect that it will be different for the population you want to examine, e.g., little children? If not, then you might want to move on to other ideas.

Promise of Future Work
To determine how promising the need/question is in terms of its connection to other ideas that you’d like to explore during your career, you may want to try putting these ideas into a concept map (or mind map) alongside research questions of interest to you. Does the idea relate to other facets within your area of interest that demonstrate clear needs for research? When you combine these ideas into a story about your research, does it hang together? Will it present a cohesive research agenda? Will you have enough to work on in the coming years?

For determining if the question/need can be translated into a study that is doable, ask yourself how will I go about knowing this? By envisioning a study, some ideas may immediately appear infeasible allowing you to eliminate them from consideration for the dissertation. For example, if a study would require a data set that is impossible to attain at this time, or a longitudinal study that couldn’t be completed by the time you’d like to graduate, you can easily sideline the idea.Most of your ideas, however, will require further exploration to assess their feasibility. When thinking about the study design consider:

  • Data:
    • Where is it?
    • How can you get it?
    • What restrictions, if any, are in place on its access and use?
  • Context:
    • Will you need to conduct your study in a specific location (i.e., in an organization, or with a specific group of individuals)?
    • How can you gain access to this organization or group of people?
    • Can you couple your research interests with the needs of the organization or group of individuals? This may make things easier for you to gain access.
  • Skills and training
    • Are there skills you will need to develop to complete the study?
    • How can you obtain training? What will it cost?
  • Other resources
    • What kinds of resources will you need to complete the study?
      This can include software, external coders you need to compensate, compensation for subjects, travel to subjects or workshops to learn skills, space for conducting interviews, etc.

At this point, you don’t need to spec it all out in detail—just enough to get a sense of its feasibility: is it, for the most part, doable? Note any hurdles as something you can discuss with your committee once you’ve settled on an idea.

Contribution to the Field
To assess the idea’s potential for contributing to the body of knowledge in the field, ask yourself what will be the outcome of my efforts? How will this work move knowledge forward, clear up inconsistencies or error, lead to the development of a new technique or tool, open new questions, improve circumstances for a particular group of individuals, etc. What kind of impact could this research have? Will other researchers and/or practitioners be interested in your findings?

Evaluating your ideas in terms of these criteria may help the most promising ideas rise to the top. These will be the ones that will rate highly in most of the above categories. (They don’t have to be highly rated in all categories.) And you can always talk those top tier ideas over with your advisor and committee members. Their input may help you single one idea out. Don’t wait to use your mentors until the day of your proposal defense. You can tap those mentors now and get their advice on how to proceed. This will save you time later on.

As you know, you can’t do everything, and that’s what a research agenda is for anyway. You can always keep a running list of questions that you want to pursue after the dissertation. Then you can jump right in and continue building that agenda on day 1 of your new job.

I also think some of the decision is gut—so don’t let the formality of my suggestion deter you from asking yourself in your gut what feels right. Just weigh it in with the more left-brain activity I’ve described above.

Good luck! I hope this has been helpful!

Dr. Laura

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