Chris Uggen's Blog: choosing projects that mean something

Wednesday, December 28, 2005

choosing projects that mean something

how do you decide which projects deserve your time and attention? i once said that i'd simply like to "contribute to knowledge" but that strikes me as vague and unsatisfying today. around my fourth-year review, i know i would have said "publishability, and step on it." yet there are always opportunity costs in beginning a new line of research, so i've tried to become at least a little more thoughtful about this.

now i ask myself (and the students with whom i work) some basic questions:

(1) does it matter? and,
(2) is it social science?
in practice, i often add
(3) would i work with a cool person? and (relatedly)
(4) what could i learn?

of course, deciding what "matters" and what is "sociological" or "social scientific" are difficult issues -- and let's not even talk about "cool" or learning opportunities. i once said "interesting," but interesting to whom (just me?)? still, the search for meaning in work seems well worth the difficulty. this is why the conversations about public sociology (and, i'm hoping, public criminology) have been so enervating for me.

while linking to the documentary in the previous post, i came across this statement from off-ramp films: "we like to do the kind of work that makes us feel good." nice. me too. their criteria do not mention anything about social science, but they seem to have some general utility:

We approach each project and work with each client with four criteria in mind:
(1) Will the project be of value in the world?
(2) Will the work be of high quality?
(3) Will it make our company more visible and help us achieve things in the future?
(4) Will it help us pay our bills?


i think they strike a nice balance between the idealistic search for meaning (does it matter? will it be of value in the world?) and more pragmatic material concerns. i especially like the focus on quality here, as this seems like a critical consideration that one cannot always take for granted. they are also future-directed, recognizing that a successful project might open doors to other things they'd like to do. in the end, off-ramp nails the sort of compromises that even the most sincere and deliberate meaning-seeker must make on the job:

If we hit on at least two of four, we can talk. Three out of four is a gimme. If it only fits one but things are slow...

wow, does that sound familiar. so how do you choose projects? you might say your choices depend on career stage (easy for you to talk about meaning, old tenured dude. i gotta get a job/promotion, so i'm attendin' to the market and will pick up the meaning down the road). but do you really think your criteria will change after you get a job or tenure or promotion or a nobel prize or a grammy or an emmy or an oscar or a big plaque with a gold star?

9 Comments:

At 8:41 AM, Blogger Goesh said...

In reading this post, what came to mind was a Prof. at the University of N. Dakota some (actually many) years ago who in a Social Problems class refused to lecture or speak to the class. He had put up a sign the first meeting saying in affect it was their class and they needed to take control of it and generate the topics of discussion and a reading list. It was 400 level class by the way. Freshmen would have probably committed suicide en masse. Anyway, the students were mute the first day I am told and slowly they started goofing-off and one fellow brought in a guitar and soon other students not enrolled in the class began to show up. I wasn't a participant but I am told they never discussed any relevant Sociology topics nor did they generate a reading list. On the last day of class he gave his analysis and observations of the 'event' and they all got a C for simply attending class. This does not solve your dilemma of course, and I suppose in today's climate, such a Prof. would be fired if not sued. Anyway....

 
At 10:31 AM, Anonymous chris said...

hmmm. that prof was either brilliant and creative or just a lazy sloth. it might be a productive experiment for a day or a week (or maybe for a graduate seminar in teaching). i try to be more goal-directed in the classroom, spelling out my general teaching philosophy and specific objectives for each course. in research, however, i can be less systematic and easily distracted by shiny new ideas. in both cases, it probably helps to have a few guiding principles. maybe a general statement of research philosophy would help keep me on-track.

 
At 12:12 PM, Blogger Goesh said...

post script - he retired after many years and though he did not set the journals on fire and take home any major awards, it is perhaps other criteria that attests to a Teacher's impact on students. A few years after his famous Soc. Problems class, his tenure was being threatened and a mob of students stormed the Sociology building and took it over for a day in protest. Some Anthro Prof. came over and did some mediating and we all went home at the end of the day. The following year he transfered to another university.

 
At 2:02 PM, Anonymous sarah said...

I was reading your teaching philosophy yesterday, Chris, while looking over the Crim syllabus. This is by far my favorite part: "Education is a service industry, but you cannot simply purchase a unit of education the way you would buy other commodities. Instead, you must devote time and energy to learning." That is just money. My spousal unit teaches at the GC and every semester has to wrestle students with this mentality. I hear echoes of the "I'm paying for this so I should get a A" mindset, shamefully, amongst other grad students, too. While I typically try to bite my tongue, internally I'm like, "don't you know that learning is supposed to be hard, in a good way?"

 
At 8:05 AM, Anonymous Anonymous said...

I think it has to do with the sort of scholar that one styles oneself after. Here's my filter:

#1 Is it a sociologically interesting problem?

[Grad student Mistake #1 is to invest in problems that aren't!]


#2 Will I get to do something completely different?

[A matter of taste, but the idea of pursuing iterations of Project X ad infinitum doesn't keep me interested. Obviously, #2 is best applied after landing t-t job and establishing a track record in an area.]


#3 Does the potential "payoff" merit the investment?

[Is it something that will result in high-profile publications? Grad student Mistake #2 is pursuing projects that will not be of interest to a wide sociological audience. Ask the faculty locally that publish in the "big journals" or with the "big presses." If they are honest, the can tell you inside of two minutes if your new project has a chance.]


#4 Will I get to leave Minnesota/the U.S. regularly in the course of this project?

[Grad student Mistake #3 is to study something of interest to only a U.S. audience (thereby dooming oneself, if successful, to travel the U.S. circuit in perpetuity). Again, a matter of taste, but I'll take the talk at Tokyo or Sao Paulo over the talk at Ann Arbor or Ithaca any day. Regular application of #4 will allow you to travel the world on someone else's dime.]

 
At 2:10 PM, Anonymous chris said...

sarah, so many of my students are overworked that it is tough to blame them for just seeing the credentialing function of education. sometimes their priorities are elsewhere. i try to get them to see its (other) real value, and most seem happy to go along for the ride. some profs resist my talk of education as a service industry, but that's exactly what it is. sometimes the students perceive us as giving lousy service because we hold them to high standards. other times, i think we just give lousy service because our priorities are elsewhere. of course, one of the services we sell is providing a rigorous environment during the transition between adolescence and adulthood. to "cave in" to students completely would dilute the value of their degrees and our services.

anonymous, who would ever want to leave minnesota? :) my research portfolio seems to have both low-risk and high-risk tracks. the low-risk track involves mining a vein of work that has proven successful and writing the logical "next" paper. the high-risk track involves taking a flier on new ideas with higher start-up costs, uncertain probabilities of visible publication, but some chance for a real breakthrough. for me, the low-risk track sometimes takes the form of "adding a new X" -- a new independent variable -- to a line of empirical research, or doing the same thing with better data or methods. the high-risk track can be "adding a new Y" -- a new phenomenon for sociologists to study -- or developing a strange new explanation for it.

[citation note: i think i'm borrowing the new-X and new-Y language from chuck halaby. he taught me a great deal about this and many other matters.]

 
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