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 second installment, featuring collected responses.

Sonia Livingstone, Professor of Social Psychology, London School of Economics & Political Science

To be honest, if an academic project doesn't make you excited, you probably shouldn't be working on it. In other words, I don't think anyone can create motivation where it doesn't exist. But what I think is more of a problem is seeing people crush or ignore their genuine motivation in order to work on a project that seems more fundable, topical or valued in the competitive world we live in. What I also see in doctoral students, too often, is a difficulty in recognizing what does, really, excite them about their projects. Over and again, in supervising, I find myself asking - what's your burning question? What do you really want to know? What do you hope, in an ideal world, your project might be able to conclude?

In my own work, I have been fortunate enough to be able to follow my enthusiasm, managing to find a way either to get a project funded and recognized, or to 'package it' in a way that makes sense to others. Still, there's often some explaining to do, to link the project I really want to do with the one that people expect, or approve of, or wish to fund. That's not always an easy part of the work, but it's better than working on something I'm not committed to! I enjoy working on things that excite other people too - then their enthusiasm is catching, and they are ready to contribute to events too.

So, I worked on audience reception of soap opera when lots of others did too. And I worked on talk shows when they seemed to be on the increase and the subject of public discussion. Since I began working on children and the Internet, I've been overwhelmed with how much interest others have in the subject, and that really helps. As my own children grow into teenagers, I find the age group that absorbs me has also got older - so there's a personal interest too. I don't mean to say, follow the fashion, as that's incoherent and may not result in a sustained body of work. Indeed, I spend quite a lot of my time writing about the consistent themes threaded through my various projects over the years, so as to identify the development of my own voice. So, if you want to be part of wider debates, it makes sense to figure out where the excitement is. If you prefer to plough your own quiet furrow, then recognizing your own intrinsic motivation is all the more crucial.

Ron Rice, Professor of Communication, U of California at Santa Barbara

That's a hard question. Several things come to mind... Meaningful research seems suited to your experience and expertise and has the potential for stimulating new areas to study. It should be an avenue that resonates with something personally relevant to you, though, in my mind, trying to avoid something so closely aligned with your personal interests that you then become unable to respond to any comments, critiques or feedback about it without taking it personally. Be cautious not to analyze, interpret, and come to conclusions that essentially reinforce your own personal beliefs and interests. Stimulating research may also be something that other people you know find interesting and/or are open to collaboration. The issue of feasibility comes into play, too -- some things maybe just aren't all that feasible given one's expertise, resources, location, etc. Identifying future research suggestions and reviews of the general area may also assist in guiding scholars to successful research projects. Looking into articles or chapters about the potential topic may provide leads on interesting or motivating ideas that others contribute about a given topic. A few thoughts on the topic!

Wolfgang Donsbach, Professor of Communications, Dresden University of Technology

Not an easy question! But certainly an important one and I congratulate you on having found such an interesting topic for your column. Here's a blurb, whatever it might be worth.

I believe that too many, particularly young, scholars run after the leading paradigms and theories in the field. This is, of course, understandable, because they think that probabilities to get their research published are higher if they work in already established thematic areas. The research questions then become smaller and also more remote and irrelevant. Young scholars should look for the research questions that lie off the beaten tracks and mainstream paradigms. And what could guide this search? As I wrote in my presidential address (JoC 56, 200) empirical research without normative goals can easily become arbitrary, random, and irrelevant. We need research that looks into the reality of accepted norms and values such as freedom, independence and equal opportunities. In short, communication research should be in the public interest. So, I would always start with "Where might we have a problem? In journalism, media use and effects, personal communication etc.?" I would not start with the question "what are the "hottest theories" according to citation rankings?"

But such a search for topics outside the mainstream must be stipulated and must get rewarded. So it is also a task for the more senior scholars, the advisors, reviewers, and deans to give gratitude to those who are going in a new direction - that might sometimes be a dead-end-street but very often an eye-opener.

Scott Reid, Associate Professor of Communication, University of California at Santa Barbara

I'm not sure about the 'passionate' part, but I've reached the conclusion that there are only three paths to discovering new research topics. 1. demonstrate that someone else is wrong; 2. expand some previous research into new territory (i.e., add a moderating variable(s)); 3. discover a phenomenon that no one else has/no one else has bothered to study.

The rest strikes me as motivational. . . for that there are lots of individual differences; culture has an affect (places with cultural vitality produce scientific knowledge as well as great art); and biology plays a role. For men at least. Scientific discoveries are predominantly made by men who are in their 20s and early 30s.