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.