Teach me how to narrow down my dissertation topic
July 11, 2013 3:55 PM   Subscribe

I am working on a PhD and in the middle of research methods classes. It's time for me to really narrow down my PhD topic/research question so that I can start focusing my assignments on my actual topic instead of random stuff. How exactly do I take my "big ideas" and give them some laser-like focus?

I'm really great at thinking of different research ideas and "wouldn't it be cool to research X?". However, everything I come up with are rather large, overarching ideas and I just don't know how to bring them down to something workable. I try thinking about it and I wind up getting overwhelmed, anxious, and get the analysis paralysis thing going, which makes me even more anxious, then I cry and think I have no idea what the hell I'm doing and I'm not smart enough to do this.

Amazingly enough, we haven't been taught this narrowing down of topics in our classes specifically (and I thought it would be part of the class but I guess not...or I totally missed it somehow). Most of my other classmates have a narrowed topic and are moving right along and I haven't even decided my final idea yet...which makes me feel terrible and useless.

Do you know of any tips, tricks, or processes to use in order to narrow down my topic? Is there a particular thought exercise I should do? Questions I should ask myself? At this point I'm looking for some specific steps to take, not necessarily ideas for research. I have a phone call scheduled with my professor (no dissertation adviser assigned yet...need a topic before that can actually happen!) but it's not until Monday and I really don't want to wait that long to get started because I'm behind enough already as it is. This is an organizational leadership program, so think social sciences and not hard sciences/lab based research.
posted by MultiFaceted to Education (12 answers total) 14 users marked this as a favorite
Response by poster: Forgot to add...I have a Master's degree but did NOT have to write a thesis for it. It was practitioner based in psychology so I took comps (and rocked them actually...for some reason I'm comfortable with that kind of stuff) but never had to write one big overarching research paper. All of my papers were class specific so I'm quite new to this research stuff (and the Master's degree was about 15 years ago anyway...).
posted by MultiFaceted at 3:59 PM on July 11, 2013

Did you take comprehensive exams? I found that was this was the most helpful process for me to see where the "holes" in the literature were. This was greatly aided by talking to others about ideas, research, concepts, etc.

I think you have to go where ever the itch takes you, in a sense. Your dissertation should be something you are passionate about. And hopefully something you've been thinking about/writing about already in classes. Start with a big question and take it to a couple of advisors and ask for their help in sorting out what is good for a dissertation and the job market.

The best dissertation is a finished dissertation. Make sure whatever question you end up with is something that is feasible. And something you are dedicated to getting done.
posted by quodlibet at 4:02 PM on July 11, 2013 [1 favorite]

Also - this thread has the mefi famous description of dissertation topic types: The driver's license vs the magnum opus.
posted by quodlibet at 4:04 PM on July 11, 2013 [3 favorites]

One thing that helped me: Begin by articulating why previous discussions of an idea or research topic you're interested in are inadequate/incomplete in some way.

Then you can flip that around and make your research project the fleshing out of a positive proposal that avoids the inadequacies you've identified or that studies a question not entirely answered in previous research.

Think in terms of augmenting an existing literature, not creating an entirely new research program.
posted by airing nerdy laundry at 4:08 PM on July 11, 2013 [4 favorites]

However, everything I come up with are rather large, overarching ideas and I just don't know how to bring them down to something workable.

The thing that I usually tell students is that a large, overarching idea isn't a dissertation topic, it's a research agenda. A dissertation topic is some specific piece of that puzzle, some specific thing that you need to show as part of your larger idea.
posted by ROU_Xenophobe at 4:26 PM on July 11, 2013 [7 favorites]

This might be one of those times when two brains are better than one.

If you have a PhD student colleague or faculty member you're comfortable socializing with, tossing ideas around for a couple of hours, causally, over coffee/beers/whatever can really help. My experience is that it's terribly easy to get trapped in your own brain sometimes as a PhD student. Someone outside of your head might be better equipped to seize on the small interesting piece within your "overarching ideas" and say "Hey....that! Tell me more about THAT thing!"
posted by pantarei70 at 4:33 PM on July 11, 2013 [2 favorites]

One thing that could help you get more specific: start thinking about the actual data level of things (if that is appropriate for your program -- I am presuming it might be, because most social social sciences entail some sort of data analysis, often questionnaire-based, ranging from specially designed ones you write yourself, to broad instruments like the US Census).

If you start thinking about what kinds of data may be available to you, you might begin to see how to formulate a very specific question that relates to your overarching ideas. It's worth looking into existing data sets first in any event; because there's no point in collecting original primary data without investigating what's already been done. But if you start from a blank slate, you'll still be paralyzed by the unlimited options.
posted by fikri at 4:36 PM on July 11, 2013 [3 favorites]

Hi! You sound like me! One thing I've found helpful is to take those broad, overarching topics and cross them with a hobby or interest of mine. An example of this based on my own experiences: the program I'm in is a practitioner-based anthropology program with an emphasis on urban settings. From the beginning I knew I wanted to focus on community development issues, but I struggled for a long time with finding a niche--a lot of my colleagues were studying food security and green infrastructure and, although I found these topics interesting, I'd become kind of bored with them because they'd been researched and presented into the ground. As an attempt to make research more fun, I wondered if there was a way to incorporate my love of visual art into my papers, which eventually developed into my current research focus--the role of public art as a participatory neighborhood revitalization strategy. It sounds all fancy but really it was just a way for me to do something that nobody else was doing and to have fun writing papers. I also talk about it a lot more passionately than I did with my earlier research.

Another strategy is to just start researching those broad topics until you come across some interesting detail that you can focus in on. I was researching a paper about queer theory in anthropology and discovered that the term "queer" has only been used in anthropological literature very recently. So what started as a paper on queer theory became a paper about the transition from "gay and lesbian studies" to "queer studies" within the discipline, and the implications of this shift. Voila!
posted by a.steele at 5:07 PM on July 11, 2013 [2 favorites]

One of my professors wrote a book, Destination Dissertation, that might be helpful for you. I have taken writing classes from her and she is very systematic and has lots of good ideas about process and organization. I haven't read this book but I am taking a writing practicum with her in the fall to write my MA thesis and I think we will use this book. The blurb on Amazon indicates that there is information about topic development. But, I also agree with other commenters who are saying to talk it through with a peer and to find something that is just super interesting to you. Dr. Foss (the author and my professor) told us in class to find topics that just made us curious.
posted by rachums at 6:21 PM on July 11, 2013

A classic way to do this is to start with a very broad statement and in 5-7 steps narrow it down to a topic . Here's an example (I'm doing this off the top of my head, but you'll get the idea):
1. (Most broad) Scholars in the field of basket making are interested in how baskets are constructed.
2. Some of these scholars are interested in hand construction of baskets.
3. Some of these scholars are interested how hand construction of baskets has changed over the past 100 years.
4. Some of these scholars focus on this changing hand construction in indigenous cultures in past century.
5. Some of these scholars are interested in this changing hand construction in indigenous cultures in the past century to better understand the hand construction of baskets as it reflects what they are meant to contain.
6. (Topic!)I am interested in the changing construction of baskets made by hand by indigenous cultures to respond to mass produced goods that are to be carried.

You can and should go through this process multiple times until you get something that excites you.
posted by Pineapplicious at 6:29 PM on July 11, 2013 [7 favorites]

How exactly do I take my "big ideas" and give them some laser-like focus? ... This is an organizational leadership program, so think social sciences

If I could go back 20 years and answer the same question for myself, I'd say ...

- Your dissertation needs to satisfy probably fewer than 10 people--your dissertation committee and a search committee. Most of them are intimately aware of how minor their own dissertations were. And there's an excellent chance you need to satisfy only your dissertation committee if you skip academia or wind up writing something else as a post-doc.
- The two topics you already know the most about are good enough starting points.
- The famous guy in your department telling you one of those topics will be huge is right. It'll turn out to be an instant tenure-track ticket, even for people doing shitty research on it.
- In fact, the second topic you know well will be big too. Yeah, you'd never have guessed!
- Other topics look cooler in part precisely because you know less about them. But you're also trying not to be someone who chooses a topic for 'personal' reasons that cause you to lack perspective. Address these impulses by going deeper into what you know (the truth is there's a lot more to be said--you only think you know what's up) and by acquiring perspective on the results from other people.
- Don't invest so much sense of yourself or your ego or whatever in the question of what to research. This only has to be better than the job you'd be doing outside academia, which--let's face it--wouldn't be rockstar glamorous either.
- The only bad choice is looking for more options instead of getting to work on what's in front of you.
- Well, it would also be bad to be immune to others' feedback telling you your research goals are too weak, but you're not even there yet.
- So, starting from something sort of familiar, ask yourself what one day of doing 'typical' research on that should look like--what are a dozen commonplace, boring things you could do with it? Be as specific as you can without naming actual studies you know of--just describe how people tend to go about addressing particular issues in this familiar topic. Which of those boring ways of addressing the topic seem ... kind of interesting?
- What would a single day of doing that typical research look like? Would you be interviewing particular people? Sending out surveys?
- What's the best result you could hope for from that dull, commonplace, yet specific research? What are the pitfalls in doing it? Can you think of a way to refine it a little to be a slightly more interesting problem? Are there cooler people to interview that haven't been interviewed yet (be as specific as possible)? Are there questions you think you know the answer to that you'd actually like to see a survey on to be sure others actually think the way you do?
- Consider standard texts and well-known results related to your topic. What sucked about them? Be specific. If you had to be their authors, how would you set up your research on the same problems?
- Gaps in your understanding aren't embarrassments to gloss over or minimize (except when writing up). At this stage, they're goldmines for research questions. Take processes you think you understand and flowchart them: you think X leads to Y, but how exactly does that happen? Are there ways to capture that happening? Where does Z come in? You aren't stupid for not knowing how to express this, even on a topic you thought you knew well.
- Everything you read for grad school, from now on, is a specific research program or set of programs waiting to happen. Take notes on how to improve bad studies. Brainstorm how to turn some work of theory or over-generalized thought piece into a list of action items (e.g. "Garry Wills, Certain Trumpets: assuming they really exist, which of these kinds of leaders could I interview in what places/jobs today? Could I develop a set of survey questions or a leadership practice inventory based on his kinds of leaders to see if they really differentiate actual leaders or tend to be covariant? Some of this seems like BS, but how can I prove it?").
- Any readings you can't conceive of as a potential action item may actually address a pretty big action item called "literature review," and you'll be grateful to yourself later if you've kept notes on what you're reading now with a view towards listing what it said in your dissertation. But for the most part, focus on texts that generate concrete questions you can operationalize.
- Texts that offer a clear contrast with what you're trying to do are helpful to the extent they continue to supply assumptions to disprove and things you'd explicitly like to avoid (by explicitly, I mean actually saying in your dissertation, "I didn't do this bad thing").
- Texts that kind of work the way you think your dissertation could work (i.e. they use methods you like and you appreciate how they went about the problem) provide analogies for what to do.
- But theory texts are bottomless. You can easily spend your entire time in grad school reading them and come up empty-handed in the end from a social sciences perspective. If you wanted to study philosophy or some other theory-heavy discipline, you should have done that. For now, just find one, maybe two reasonably current theoretical works you think you can use to explain some things, even if (or, rather, especially if) you can create problems in other parts of the theory.

Whew, I guess I've had a while to think of things I did wrong or poorly. It worked out well enough in a "rich inner life" sense that I don't actually regret how I spent my time in grad school, but it for sure wasn't optimal with respect to the goal of narrowing down a topic into specific research questions.

How my dissertation actually turned out is I cobbled a few mediocre questions and, uh, data points together at sort of the last minute based on one of those topics I knew well at the start and could have refined into something better, if I'd just gone with it initially and spent more time trudging through it and throwing away successes no worse than what I actually wrote up in the end.
posted by Monsieur Caution at 7:50 PM on July 11, 2013 [5 favorites]

You want to narrow down the research topic enough to make the research manageable. Localize it, if possible to a state or city. Focus on something that has enough data to make an analysis possible but not an overwhelming amount of data that will make analysis a life-long endeavor or only possible with a million dollar grant. Don't narrow it down to the point where it is extremely esoteric.
posted by JJ86 at 6:03 AM on July 12, 2013

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