Proceedings of the First AAAS Technology Education Research Conference
Towards a Research Agenda
Andrew Ahlgren
Project 2061
American Association for the Advancement of Science
On at least two occasions I have been involved in research-agenda conferences
in science education. In both, the output was to endorse everything that anyone
was already doing. It is entirely possible to spend a career doing research
for the fun of it (or the publication credit) without seriously considering
how it might be useful—or what might be more useful. Because there are
nowhere near enough time and resources for all the research we can think of,
or even all that we would like to do, not having priorities is tantamount
to saying that the research doesn’t really matter much.
A model in science education?
Science-education research has been far more voluminous than technology-education
research, but is not necessarily a good model. The mass of the research before
1970 was of very little value, because educators just had not recognized the
most powerful tool for understanding teaching and learning: What and how students
think and learn. The vigorous "quantitative optimism" of researchers
was premature, for they had not yet identified the important variables to
study. Method-A-vs.-method-B studies had little hope of shedding light on
learning (and usually resulted in "no significant difference").
Just finding out what students already think is difficult.
The source of students’ difficulties in learning even one idea or skill
can be very puzzling; researchers find that it may take a year or more of
studying students to figure out just what the problem is. And even then there
is no guarantee that the nail has been struck on the head. But identifying
common problems in student thinking isn’t tantamount to knowing what
to do about them. Researchers who thought they had uncovered problems and
modified instruction to ameliorate them are often frustrated by the resilience
of the students’ naïve ideas.
Yet, it should be said, lack of progress did not keep science-education researchers
from flourishing professionally. Camps sprang up, journals proliferated, national
conferences were established, and a cultural identity evolved. All with little
enlightenment on how to teach students well. A good example: studies of the
value of laboratory in school science have been going on for over a hundred
years, and the literature is a mostly incoherent collection of different goals,
different settings, different measures, and conflicting results. By and large,
no benefits—in understanding ideas, appreciating the nature of science,
or positive attitudes toward learning science—have been demonstrated
other than "finger skills." (For example, the skill of pouring water
from one test tube into another will obviously improve with practice.) No
reliable answer yet.
So even good research does not point inexorably to good instructional practice.
Nevertheless, some excellent research has been done in the last two decades
or so on how students understand topics in science and mathematics. It is
this aspect of science-education research that can be most profitably copied
in technology education.
Consider, for example, this passage from the Benchmarks for Science Literacy
(1993) chapter "The Research Base":
Newton's laws of motion. Students believe constant speed needs
some cause to sustain it. In addition, students believe that the amount
of motion is proportional to the amount of force; that if a body is not
moving, there is no force acting on it; and that if a body is moving there
is a force acting on it in the direction of the motion (Gunstone &
Watts, 1985). Students also believe that objects resist acceleration from
the state of rest because of friction—that is, they confound inertia
with friction (Jung et al., 1981; Brown & Clement, 1992). Students
tend to hold onto these ideas even after instruction in high-school or
college physics (McDermott, 1983). Specially designed instruction does
help high-school students change their ideas (Brown & Clement, 1992;
Minstrell, 1989; Dykstra et al., 1992).
Research has shown less success in changing middle-school students' ideas
about force and motion (Champagne, Gunstone & Klopfer, 1985). Nevertheless,
some research indicates that middle-school students can start understanding
the effect of constant forces to speed up, slow down, or change the direction
of motion of an object. This research also suggests it is possible to
change middle-school students' belief that a force always acts in the
direction of motion (White & Horwitz, 1987; White, 1990). (p. 339)
This passage illustrates some important aspects of a research program: multiple
researchers, in multiple institutions, are involved in studying the same important
concept; the study is sustained over time; and cognitive investigation is
supplemented by trials of instruction that take account of it (and typically
lead to more of it). Another important point evident here: though educators
often make the assumption that things can’t be too bad, for after all
the students are learning some things well enough, that assumption (in science,
anyway) is obviously faulty.
The text of Benchmarks for Science Literacy—which includes
specific learning goals in the chapters "The Nature of Technology,"
"The Designed World," "Common Themes," and "Habits
of Mind"—can be found
at the AAAS Project 2061 web site.
Some simplistic examples of coherent agendas for research
So what agendas for research in technology education might make sense? The
main tenets are: there are far more interesting research projects than there
are researchers and time to carry them out; and we can expect useful results
only if we focus on limited strategies. So tough decisions have to be made,
if there is to be any substantial progress. Here are some admittedly simplistic
examples of what coherent agendas for focusing research might look like:
A. Replicate promising findings in many different labs and contexts, to see
how generally valid they are. (This in contrast to everyone choosing his own
favorite—and perhaps unique—topics, activities, and measures.)
B. Just the opposite. Cover the widest possible range of research questions
that can be imagined. (Little progress would likely be made for a long time
in any of them, but general patterns for methods could be scoped out.)
C. Track students over multiple years, to be able to describe how student ideas
and skills develop over time—and get hints about what may have helped.
(This costs time, and delays research papers, but may in the long run be a
very valuable direction.)
All of these examples assume that student learning is by far the highest priority
to study. (If we don’t know how students learn, then all the potentially
supporting attention to attitudes, variations on design activities, curriculum
surveys, professional development, and social setting research seems pretty
pointless.) But this was only an exercise, not yet a proposition for any particular
research agenda.
Clearly, it will not be acceptable to endorse doing all the things we are already
doing, and maybe more besides. No doubt multiple methods can be helpful. Case
studies, for example, are probably going to be more useful for a while than
statistical surveys of what happens to be being done now. But case studies
should not be driven by fondness for particular activities, as seems most
often the case now, but rather by how students learn particular ideas and/or
skills. The rationale is not "Here is this activity I like, so I’ll study
how it works" but rather "Here is this skill I think is important, and I’ll
study how it’s possible for students to learn it." In either case, particular
activities will almost certainly have to be involved, but the perspective
on them will be very different.
