CS Majors are least likely to finish degree among Science majors

“Of the STEM fields, computer or information sciences had the lowest rate at 46.4 percent.”  Maybe lots of CS faculty agree with the commentor to the last blog post, that it’s better to flunk out CS students than let them graduate and suffer the pains of being a computing professional.

All significant education questions are economic

Seymour Papert once said, “All the interesting questions in education are social questions.”  I heard this when I was visiting his company, Logo Computer Systems Incorporated (LCSI) in Montreal in the early 90’s.  His point was that what was really interesting was now whether or not Logo “worked,” but why was it being taught or not taught, what did society value and how did that get reflected in schools, how were teachers trained and then valued by their society, and so on.  He found that the education questions that most interested him were actually about the societies in which the education occurred, and what that told him about the choices of that society.

I’ve been thinking about Seymour’s comment while thinking about my last blog post, about the research questions surrounding Media Computation.  This leads me to Guzdial’s Claim: All significant education questions are economic. (By naming it, we make it easier to refer to it and refute it.)  Those education questions that lead to wondering about society are interesting, but they don’t lead to change.  A significant question, as I’m defining it here, leads to change.  Change in education is all an issue of economics.

We know how to get education right.  If we have a good tutor for every child who wants to learn, learning will occur.  Bruner tells us that anything can be learned in an honest way. Thus, one tutor per child can lead to any kind of learning. However, we can’t afford that.  Everything else we try is an economic compromise over what we know will work.

Economics is not about money.   A nice definition of economics (cited in the Wikipedia article) is “the science which studies human behaviour as a relationship between ends and scarce means which have alternative uses.”  Human time and attention is a scarce resource that could be used for alternative pursuits.  “What do students choose to study?” is an economic question.  “Why do teachers teach that?” is an economic question.  They’re making choices.  If you want to change something significant in education, you have to know why people are making the economic choices they’re making, and figure out a way to make your alternative more attractive.

The questions that Media Computation was designed to answer were economic ones.  Losing 30-50% of the students in a CS1 is a huge waste of resources.  That’s what we tried to address.  It’s interesting is how the contextualized approach impacted future student choice.  Did we convince students that computing is interesting?  I don’t think so.  Instead, we convinced students that computing was relevant to the things that they already had value for, that it had utility for them.  Thus, we had students who were willing to take “More Media Computation” classes (as long as we kept explaining the utility), but not “More Computer Science” classes.

What I find myself struggling with here is how to describe design questions in education.  Is it significant or interesting to design a better way to teach something? If your better way is trying to address economic issues, I am claiming that it is significant.  Is it important, interesting, or worthwhile to figure out how to teach something simply better?  And what does that mean to do better?  Can you do better than the tutor with the good student?  We don’t currently have good measures of what “better learning” in computing education means.  When I look at my favorite textbooks (Structure and Interpretation of Computer Programs and Computer Science Logo Style), I have a hard time saying that they were “significant” — few teachers ever used them, few students know about them today, and the languages they use have fallen out of favor.  (We CS teachers are so driven by fads.)  SICP has always been expensive to implement because it often increased WDF rates. While SICP was used to teach many of the leaders in computer science today (since it was used at MIT, Berkeley, and Brown), it’s hard to measure the impact of the approach.  Was SICP significant for those leaders?

I have certainly seen design questions answered in insignificant ways.  I get frustrated with people who show me their “great new way of teaching X” that “my students and Girl Scout groups really love,” and when I ask them for their evidence, they have none.  “I talked to the students” or “I could tell”  or “Look at the cool thing they built” is the best that I get. Teachers are lousy probes.  A teacher is not good at telling how students are learning or engaging, just by talking with them.  Measurement should be uniform across students to get any kind of sense of what of significance is happening.

As you can tell, I’m struggling these days with what makes for worthwhile education research questions.  What is the value of education design, development, and research?  Is it possible to have long-term findings?  Economic conditions (e.g., what students and teachers value) change regularly.  Is it possible to come up with a curriculum that could be used successfully for more than 20 years?  Or is curriculum always churning, to keep up with changing values and choices? What would be a significant education research question whose answer would be useful 100 years from now?  Do we have any that we can point to?

Within computing education research, doing something of worthwhile significance becomes even more dubious.  If you doubt that all significant computing education questions are eocnomic, come up with a non-economic explanation for changing our CS1 language every 5-10 years!  It’s certainly not because we have evidence that students learn better with the new language.  Computing education research questions that have any significance, that can lead to change, are economic ones.

Media Computation is not “done”

I heard from a colleague last week that Media Computation is “done.”  “There are no more research questions to answer.  No one will be able to publish on it anymore.”  I’m at a Media Computation workshop in Kansas City this week where I can assure you, nobody thinks all the questions about Media Computation are answered.

What we do know is that adoption of Media Computation (at multiple schools, with both genders and a variety of ethnic groups, including under-represented minorities) has improved retention in the first course compared to the more common approaches to CS1.  That was our explicit goal in designing Media Computation, to address the 30-50% WDF rate.  While that’s a pretty often-repeated result now, I still wonder what that means.  Is Media Computation “teacher proof”?  Could a really lousy teacher do a really lousy implementation that does not improve retention?  Well, of course!  So, what then does that finding mean?  It’s a true statement empirically, and it’s telling us something about what engages and motivates students.  I’m not sure what it tells us about computing education and its practice yet.

What are the other open questions?

• Does Media Computation lead to the same learning? I don’t know.  Nor does anyone else have evidence of their CS1 approach leading to the “same learning.”  We have no way to measure “same learning” across languages and approaches. We are behind other domain-specific education research fields.
• Does Media Computation lead to more interest in computing as a major or minor? The evidence that I’ve seen suggests “no,” and further, there’s not much that we can do with any new approach at the undergraduate level to influence our enrollment numbers.  Sarita Yardi and Amy Bruckman’s ICER 2007 paper suggests to me that decisions about whether computing is a promising career are made by students in their pre-teens.  That meshes with what we’re seeing in our Girl Scout and high school studies.
• Does Media Computation lead to more interest in going on to more computer science classes? I don’t know.  We did have enough interest in our CS1 to build a CS2.  Bryn Mawr is finding that their IPRE approach in CS1 is leading to their largest CS2’s ever, which is using a context of robots and media.  I’m not sure how one would go about answering this question in a way that generalizes across schools — it’s an interesting question.
• What’s the real impact of Media Computation or any contextualized computing approach past the first semester? That’s a hard, interesting, and open question.  Mike Hewner answered this question in one way in his ICER 2008 paper where he studied Georgia Tech seniors and asked them (indirectly) about the impact that their contextualized first course had on the way that they used computing over the rest of their academic career.  Bottomline: Not much.  If you use computing in your other classes, than that first course was useful and spurred on your interest.  But if your major doesn’t use much computing, then that first course may have been enjoyable, but it was one course out of 40 that you took in your undergraduate years — why should that have made much difference?  On the other hand, Lana Yarosh’s paper suggests context is still useful in CS2, and we had a paper in JERIC last year showing the benefit of context in a computer organization class.  Context may still be useful, but maybe different contexts.

What is a contextualized computing education approach, anyway?  Is it just problem-based learning applied to computing? Project-based learning?  Is it “teaching with a theme” as Bill Gates says has been so successful with the high schools funded by the Gates Foundation?  What kind of contexts/themes lead to improved engagement, and which don’t?  Do contexts have to change with generations of kids?  Is that why our generation did fine without contexts (unless computing the next Fibonacci number is a “context”) but we’re seeing an impact of context on this generation?

No, I don’t think MediaComp is “done” yet.  It’s actually a bit worrying that teachers or researchers would think that it is.  That’s all the evidence you need?  You’ll accept something as being “known” with what we have so-far?  As computing education researchers, we should have a higher bar.  It’s one thing to say “It’s no longer interesting” or “It’s pretty clear what direction the results are pointing now.”  It’s another to say that “We know all that we need to know.”