But, we’ve become too timid in many of the ambitions we collectively and individually have for our field.
I start to come to that conclusion when I hear from our Program Directors that too few of the proposals they see offer truly innovative ideas that excite panels or themselves. While confirmatory or incremental work is essential, we must also have a continuous flow of exciting, innovative ideas (and the community must ensure they are well received, and then we must ensure they are funded).
I am even more convinced that we need to regain the excitement that brought many of us to the field when I hear the incessant—but clearly important in the near term —discussion of why CS enrollments are falling, focusing on whether there is too much math required (probably not, IMHO) or whether we need a big ad campaign (probably, but to advertise what?) or worse, whining about why field X is getting more funding than field Y (both within CS and in comparing us to other fields).
I definitely conclude that we need to regain our grand aspirations when I review the entire NSF portfolio in detail each year and see the deep and often grand quests of other fields—quests with no discernible practical result that may take decades of dedicated and fundamental work, involving theoretical work that will break entirely new ground, or requiring grand experimental projects that may total billions of dollars.
I absolutely know that there is something fundamentally different about the tenor of much research today when I think about the visions of even a few of the giants of our field like Doug Engelbart, Alan Kay, Herbert Simon, Carver Mead, Gordon Bell, or Juris Hartmanis—just to name a few from among a good many more that had (and still do!) truly grand and audacious ideas.
Where are the BHAGs (Big Hairy Audacious Goals) of today?
As we are developing the Computing Community Consortium 1 and as I talk with many computer scientists at all levels, the question of the vitality of our field springs out. That question should concern every one of us, most especially those of us in positions of leadership. It is a question for which there are multiple answers and multiple rejoinders—all of which deserve to be heard and explored.
Let me comment briefly on the current national focus on “innovation.” I believe all of you would agree that it is a long-overdue and very important step. Whatever disagreements one might have with the American Competitiveness Initiative (ACI) 2 I hope that you will join me in applauding, supporting, and strengthening it.
Computer science and the applications it has spawned can rightly claim to have been the engine of much of the innovation that has been driving the U.S. economy in recent years. While the “irrational exuberance” of the late 1990s led to the crash of many ventures, the underlying theme of innovation in the IT industry—and those industries whose operations are now enabled or enhanced by IT products—has continued more or less unabated. Likewise, utilizing CS as a peer in a number of research activities is leading to fundamental innovations throughout science and engineering.
Doesn’t this demonstrate the vitality of our field? Doesn’t this deny my assertion that we may be too timid in our goals? At one level it does—until you ask what fundamental concepts and research these innovations depend on when you trace back their developmental history.
More to the point, where are the fundamental changes in computer science?
If you ask that question, then I believe that you will agree with those who are now successfully pushing for more fundamental research in science in general. 3 The basic message is that we are in danger of losing the kind of edge we have in end-result innovation in this country because we are not asking deep enough questions and pursuing the BHAGs.
We need to explore entirely new concepts and we need to do that in new ways, whether in theoretical and small-scale research or large-scale experimental projects. Fundamental results typically start in relatively small, even individual, efforts. We must not forget that, but just because a project is small-scale doesn’t mean that it will result in entirely new concepts. As an example, the Science of Design effort 4 is intended to break us out of a box regarding how to develop software.
At the same time, it is essential to employ experimentation wherever possible to enable the kind of future usage of CS concepts that the world is madly rushing toward, but won’t be able to reach solely with today’s stock of fundamental ideas. Further, experimentation need not be limited to the systems builders. If you draw parallels to physics—where huge experiments are carried out to validate a theory—or astronomy— where observations lead to theorizing—and note that in both cases there is then a “virtuous cycle” between the two modalities, then I hope you see the opportunity for computer science. Indeed, some already have. 5
A new modality of experimental research in a number of CS fields may be possible, and it may require substantial instrumentation (in NSF lingo) to carry out. We should not be timid in conceiving of, planning for, and requesting such research infrastructure, just as other sciences routinely do. The Computing Community Consortium described elsewhere in this issue is expected to do exactly that over time for all areas of computer science.
An example of this kind of instrumentation is the Global Environment for Networking Innovations (GENI) initiative. It is an instrument for use by CS researchers in doing their fundamental, experimental research. This demands that it be open and accessible for measurement and for ad hoc changes at all levels and in all aspects. We are currently seeking community input to make sure that this is the case. This is essential to experimentation, and is a fundamental requirement that we are placing on the design.
Another way to look at such instrumentation-intensive projects is as prototypes for future practical and operational IT-based artifacts. We have ample precedents in our field in which research artifacts ultimately turn into products that turn the world upside down. Do you remember what SUN stands for, or know where Google developed, or understand the role that TheoryNet/CSnet/NSFnet played in creating today’s Internet?
But, our primary objective should remain to push forward our scientific understanding of computation and the devices/systems that instantiate our theories.
While that may happen in the case of an infrastructure-intensive project—and then again, may not—it often begs an important set of questions from those who pay for research along the lines of: “How are you going to transition results into the practical world?” There are two answers to that question: one short term and one deeper, but both important.
The short-term answer is that as important as “technology transfer” is, our mission is to advance fundamental research. Given that there are any number of fundamental things we don’t understand about the structure and operation of complex IT systems, we believe that attempting to develop such an understanding is valuable in its own right. Just as other fundamental scientific questions engage legions of people and tons of money for decades, we believe these questions stand on their own as worthy of investigation.
Nonetheless, as a practical matter, we must pay close attention to the issue of how we can enhance the ultimate transfer of results into more practical results. Our field and the industries it has spawned have a rather good record, in fact, of rapidly making money and improving lives with ideas and theories and prototypes that were in the lab or being talked about at academic meetings only a few years ago—the examples are abundant.
The deeper answer is one that is important to understand as we collectively try to advance our field. Computer science is not science, not engineering, not math—but a combination of all three. That is hardly an original observation, but the rub is that because we are a new field (yes, new even though some of us have been in the field almost half a century) we are still working out just what that answer means in terms of what we do as researchers and educators. Do some of us belong to just one of those fields, but still call ourselves computer scientists? Do we do math or science at one phase of research and engineering at another? Do we do something that is somehow a bit of all three and we just can’t describe how that works? Did we originate in one field and are moving toward another?
When I think about the vitality of our field, I’m less interested in an abstract answer to these questions than I am in helping determine what we should be doing. In that context, I believe we have lost some of the original vision and vitality of the founders of our field who were not afraid to ask big and deep questions, and to experiment where appropriate to find the answers to their questions. To some extent I think we have lost our way as scientists and let the inner engineer (and entrepreneur!) in each of us become too ascendant.
The questions our field truly faces are not questions of why students don’t love us or why decision makers don’t give us enough money—they are the exciting, compelling questions of understanding some of the most complex artifacts ever created (or discovered, for that matter) and of attempting to create new theories, understandings, and artifacts that far transcend anything we have today.
As a professor, dean, and now research funder, I well understand many of the factors that push us toward the safe, rather than the innovative, path in research and education. If there was ever a time to overcome and ignore those factors—at all levels—it is now.
We all have an important role: Those of us at funding agencies and research labs must set higher expectations and educate our colleagues on the importance of our research and education; academic and lab administrators must reward true advances, not just incrementalism; and, most importantly, each researcher and educator must continually strive to contribute to the advance of our field in fundamental ways.
Don’t be timid!
1 See the March 2006 issue of CRN, as well as the article on the Computing Community Consortium in this issue.
3 See Rising Above the Gathering Storm www.lab.nap.edu/books/0309100399/html/11.html
5 See www.cs.yale.edu/homes/jf/tonc-agenda-draft.pdf for what the CS theory community is doing and www.nsf.gov/funding/pgm_summ.jsp?pims_id=13679&org=CCF&from=home for what part of the communications community is doing.
I look forward to hearing from you. Please send general comments to me at pfreeman [at] nsf.gov.