The NAE's Grand Challenges vs. Mine

March 30, 2008 · Venkat
The US National Academy of Engineers recently released a list of 'Grand Challenges.' As you've no doubt noticed, this sort of top-down driving of research agendas has picked up pace recently. You also have the new X-prize for a 100mpg car, following on the heels of the one which Burt Rutan won for commercial space flight. A bunch of other X-prizes have also come into being. Google joined the fray with its Lunar X-prize. Consider also the DARPA Grand Challenges. Then of course, there are the Clay Millenium problems in mathematics. Something bothers me about this top-down agenda setting for research, and formal competition as a way to drive innovation. Let's poke at it by comparing the NAE's list with mine. First, the NAE's list (you can find a detailed site here):
    1. Make solar energy affordable
    2. Provide energy from fusion
    3. Develop carbon sequestration methods
    4. Manage the nitrogen cycle
    5. Provide access to clean water
    6. Restore and improve urban infrastructure
    7. Advance health informatics
    8. Engineer better medicines
    9. Reverse-engineer the brain
    10. Prevent nuclear terror
    11. Secure cyberspace
    12. Enhance virtual reality
    13. Advance personalized learning
    14. Engineer the tools for scientific discovery
      The NAE's description talks about the process of selection thus: "The panel, some of the most accomplished engineers and scientists of their generation, was established in 2006 and met several times to discuss and develop the list of challenges.Through an interactive Web site, the effort received worldwide input from prominent engineers and scientists, as well as from the general public, over a one-year period.The panel's conclusions were reviewed by more than 50 subject-matter experts." Now let's look at my list (much shorter) and think about the differences -- I wouldn't pose mine as grand challenges for humanity, but simply as a set of questions that make me personally curious. I'd like to see them solved during my lifetime just to learn what the answers are, and possibly work on them myself if I can ever create an opportunity:
      1. A purely audio UI that is as effective as visual GUIs
      2. Secure single logon/identity for all online activity (including financial)
      3. Realistic conversational computer games (simulating talking to real humans)
      4. Truly modular lego-like electro-mechanical engineering systems
      5. Self-replicating machines that can live in junkyards
      6. Simple method to count calories automatically (for example, by simply taking a cell phone picture of any food I am about to eat)
      7. A legal innovation that treats machines of a certain level of hardware+software complexity as autonomous legal entities (like corporations)
      The Difference In my mind, the key difference between the two lists is the level of unpredictability. Nothing on the first list is particularly surprising, and most well-informed technologists can instantly appreciate why the problem is on the list. Now, my list, whether or not it represents important problems is, I would argue, less predictable. There are other differences: my list is  more specific, and where there is overlap (for example, NAE's 11 with my 2, and if I explained more, you'd see that my 3 overlaps with their 13), my questions are both more specific and framed differently. The difference arises because democratic, consensus-seeking processes tend to gradually eliminate variety and novel framings of issues. The NAE's list is not dull and boring in spite of the luminaries involved. It is dull and boring because of the luminaries involved. Individual technologists on the other hand, will usually only put on their list problems they've thought and been excited about for a while, and for which they see some promising framings and lines of attack. This is why Hilbert's problems, as opposed to these ''committee'' problems, had such an impact. The NAE's list worries me for two main reasons. First, in my opinion, more than half the effort in innovation is seeing and framing the problem the right way. Dull, predictable framings lead to wimpy answers. Second, it focuses on weaknesses -- problems where technology hasn't gained much traction. Think about it: fusion and solar energy have been major challenges in our minds for decades now, yet in the last few decades, the biggest advances haven't come as a consequence of these big-ticket worries. The Internet, the Web and microelectronics came about because people found an aspect of nature where work yielded quick and escalating returns in surprising forms -- strengths of our technological system, so to speak. I will make my own prediction: in 50 years, the top 10 innovations we identify for the period 2008-2058 will have very little overlap with the NAE's list.