Graduate students everywhere have a common goal: to find a meaningful research topic. At the last meeting of the International Communication Association in San Francisco, members of the Student Affairs Committee asked us to write a column featuring advice on how students might find and pursue meaningful research topics.

We invited several established scholars who are passionate about their work to give us their advice. Below is the first of four installments featuring their collected responses.

Michael S. Stohl, U of California at Santa Barbara
(author (and coauthor) of several books and articles related to political communication, terrorism, and human rights. Professor Stohl has received numerous research awards, some of which have included Fulbright Fellowships and visiting Research Grants, to name a few.)

The sources of research topics about which people are passionate are many and varied. Some scholars find them in the context of reading a scholarly article and seeing a critical connection that enables a theoretical leap or a methodological transformation. Others are touched by a social problem and realize that they have the theoretical and methodological tools to contribute to better understanding and perhaps the ability to make a contribution. In my own case the discovery of my first area of sustained research arose while I was an undergraduate searching for a book in the library stacks and happened across a book titled The French Revolution in English History. It stimulated my thinking on how something that happened in another country could have so profound an effect elsewhere. It led to me thinking about what we now call globalization processes and their impact on domestic conflict and state repression. I have studied all three of these areas ever since.

Sharon Mazzarella, Clemson U
(editor of the book 20 Questions about Youth and the Media and founding coeditor of the journal Popular Communication, who has published widely on girls and the mass media.)

If you're anything like me you know the experience of being "jazzed" when you return home from a conference-especially if that conference is ICA. I've been attending ICA for almost 25 years (EEEK!), and have never failed to leave with a renewed excitement about the discipline in general and about potential research projects in particular. Whether that excitement stems from a dynamic audience Q & A following my own presentation, from things I've learned while attending other panels, or from having my intellectual horizons expanded by meeting cutting-edge scholars at one or another social event, I have found that the best way to reenergize intellectually and generate new project ideas is to immerse myself in the conference experience. In fact, it's not unusual for me to leave a conference with three or four project ideas swirling around in my head or with plans for collaborations with other scholars. Certainly not all of these projects and collaborations come to fruition, but some do, and those are the ones that matter because, invariably, those tend to be the ones that are both the most exciting and the most doable. There is nothing like that feeling of postconference jazz to stoke my intellectual fire and to keep me passionate about my work.

Robin L. Nabi -U of California at Santa Barbara
(Author of many works on the interplay between emotion and cognition in understanding effects of mediated messages.)

How do you discover research topics you're passionate about pursuing?

I think it's ultimately about exposing yourself to lots of different ideas and seeing which feel exciting to you. As you begin to pursue those ideas, you might find that you end up going in a direction that's not what you expected. As long as you're enjoying the process, that's just fine. If trying to answer the question doesn't thrill you, it may be time to find a new one. This isn't to say that if you don't enjoy every moment of your research, it's time to move on. Rather, the idea of pursuing that research should be exciting, even if the specific tasks may at times feel tedious, frustrating, overwhelming, or otherwise onerous. By the way, I think the ICA conference is a great venue to embark on this sort of discovery. With hundreds of ideas being presented, you can pick out the panels and papers that sound interesting over the course of the weekend and see which ones you most enjoy and still think about after the conference ends.

Michael Morgan, U of Massachusetts
(co-author of the book Television and Its Viewers: Cultivation Theory and Research and author of many other works on television, socialization, and enculturation.)

At the risk of sounding trite, I'm tempted to say that you if you go looking for "meaningful research topics," then you'll never find one - rather, if it's something that's going to ignite and sustain your intellectual passions, it will find you. Something clicks, sets off a spark, and engages you - you just know it when it happens. And to completely contradict myself, you can't just sit around and wait for cosmic forces to deign to anoint you with their inspiration. You've got to read, talk, ask, listen - so you don't try to reinvent the wheel - and carefully think about the Big Ideas (and their associated nitty-gritty implications) that really excite and fascinate you, and that led you to want to go to a research-oriented grad school in the first place.

In my experience, most grad students have at least a general idea of what they want to focus on (sometimes it's too general, sometimes it's too specific; too often it's driven by method rather than theory). I learned in grad school that the best way to do something "meaningful" is to continually ask yourself, "So what?" Why is this an important topic, why will the world be a better place because of my findings or conclusions? But at the same time, I've seen too many grad students wait, and wait, for the "perfect" dissertation idea to come to them. There's no such thing, and part of the task is to choose something that's workable and feasible - from a wide range of possibilities - and then sink your teeth into it.

And if you do a reasonably good job of studying something, then in the process you will most likely raise more questions than you answer, which can ideally lead to a long-term research program. Think about building a coherent research trajectory - not one that is narrowly and linearly focused but one that can evolve as each step leads to possibilities for developing further inquiries. (I say this while recognizing that one of the most appealing aspects of academic research is that it opens spaces to go off in entirely new directions at any time.) In my own research, the constant transformations in media technology and policy, and the immense complexity of studying effects, have automatically provided me with an ever-changing landscape that continually raises new questions and issues; in that sense, I have expended no effort whatsoever in trying to sustain my own interest level. I am shocked when I realize that I have been working in this area for over 30 years; it feels like a fraction of that.

In our next column, we will feature more advice on this topic. Are you a senior scholar who would like to weigh in on this discussion? If so, please e-mail us at rhains@salemstate.edu and mmarlow@uidaho.edu.