WHEN THINGS START TO THINK | Chapter 12: The Business of Discovery

May 15, 2003

Originally published by Henry Holt and Company 1999. Published on KurzweilAI.net May 15, 2003.

There used to be quite a demand for psychic mediums who would go into “spirit cabinets” and channel fields to contact lost souls who would communicate by making sounds. In my lab, once we had developed the techniques to induce and measure weak electric fields around the human body, we realized that we could make a modern-day spirit cabinet (well, everything but the lost souls part). So of course we had to do a magic trick, which we were soon working on with the magicians Penn & Teller, who were planning a small opera with Tod Machover. We expected to have fun; we didn’t expect to save the lives of infants, or learn something about how industry and academia can remove technological barriers by removing organizational barriers.

The hardware for our spirit cabinet was developed by Joe Paradiso, a former experimental particle physicist who in his spare time builds electronic music synthesizers that look just like enormous particle detectors. Joe designed a seat that radiates a field out through the medium’s body, and from that can invisibly measure the smallest gestures. Tod shaped a composition for it, and Penn & Teller toured with it.

The trick worked technically, but it ran into an unexpected artistic problem: audiences had a hard time believing that the performers created rather than responded to the sounds. Science fiction had prepared them to believe in hyperspace travel but not in a working spirit cabinet. It was only by sitting people in the chair that we could convince them that it did work; at that point we had a hard time getting them back out of it.

I saw this project as an entertaining exercise for the physical models and instrumentation that we were developing to look at fields around bodies, not as anything particularly useful. The last thing I expected was to see it turn into an automotive safety product. But after we showed it, I found a Media Lab sponsor, Phil Rittmueller from NEC, in my lab telling me about child seats. NEC makes the controllers for airbags, and they were all too familiar with a story that was about to hit the popular press: infants in rear-facing child seats were being injured and killed by airbags. Deaths were going to result from leaving the airbags on, and also from switching them off. Finding a way for a smart airbag to recognize and respond appropriately to the seat occupant was a life-and-death question for the industry.

No one knew how to do it. To decide when to fire, the seat needed to distinguish among a child facing forward, a child facing reverse, a small adult, and a bag of groceries. Under pressure to act, the National Highway Traffic Safety Administration was about to mandate a standard for disabling the airbag based on the weight of the occupant, an arbitrary threshold that would be sure to make mistakes. The only working alternative imposed the unrealistic requirement that all child seats had to have special sensor tags installed in them.

Phil wondered if our fancy seat could recognize infants as well as magicians. My student Josh Smith veered off from what he was doing for a few weeks to put together a prototype, and to our very pleasant surprise it not only worked, it appeared to outperform anything being considered by the auto industry. After NEC showed the prototype to some car companies they wanted to know when they could buy it. NEC has since announced the product, the Passenger Sensing System.

It looks like an ordinary automobile seat. Flexible electrodes in the seat emit and detect very weak electric fields, much like the weak fields given off from the cord of a stereo headphone. A controller interprets these signals to effectively see the three¬≠dimensional configuration of the seat occupant, and uses these data to determine how to fire the airbag. The beauty of the system is that it’s invisible and requires no attention; all the passenger has to do is sit in the seat. Although the immediate application is to disable the airbag for rear-facing infant seats, in the future the system will be used to control the inflation of an airbag based on the location of the occupant, and more generally help the car respond to the state of the occupant.

Now I would never have taken funding for automobile seat safety development—it’s too remote from what I do, and too narrow. NEC would never have supported magic tricks internally—it’s too remote from what they do, and too crazy. Yet by putting these pieces together, the result was something unambiguously useful that we probably could not have gotten to any other way. This is one of the secrets of how the Media Lab works with industrial sponsors: maximize contact, not constraints.

That’s what much of academia and industry carefully prevent. The organization of research and development in the United States can be directly traced to an influential report that Vannevar Bush wrote for Franklin Roosevelt in 1945.

Two technologies developed during World War II arguably ended the conflict, first radar and then nuclear bombs. These were created under the auspices of the then-secret Office of Scientific Research and Development, directed by Vannevar Bush. After the war President Roosevelt asked him to figure out how to sustain that pace of development for peacetime goals, including combating disease and creating jobs in new industries.

The resulting report, Science—The Endless Frontier, argued that the key was government support of basic research. Both nuclear weapons and radar were largely a consequence of fundamental studies of the subatomic structure of matter, the former directly from nuclear physics, and the latter through the instruments that had been developed for nuclear magnetic resonance experiments. Just when science and technology emerged as a key to economic competitiveness after the war, the country was facing a shortage of scientists and engineers who could do the work. Attracting and training them would be essential.

Vannevar Bush proposed that the government’s postwar role should be to fund curiosity-driven basic research studies. These should be done externally, at universities and research institutes, and be evaluated solely with regard to their scientific merit without any concern for practical applications. Since the direction of true basic research can never be predicted, the government would provide long-term grants, awarded based on the promise and record of a research project rather than claims of expected outcomes of the work. Researchers doing solid work could expect steady funding.

The useful fruits of the basic research would then be picked up by applied research laboratories. Here the government would have a stronger role, both through the work of its own agencies, and through fostering a regulatory climate that encouraged industry to do the same. Finally, the applied results would move to industry where product development would be done.

He proposed the creation of a new agency to support all government research, the National Research Foundation. By the time the enabling legislations was passed in 1950 the title had changed to the National Science Foundation (NSF) since there were too many entrenched government interests unwilling to cede control in areas other than basic science. Vannevar Bush thought that a staff of about fifty people and a budget of $20 million a year should be sufficient to do the job.

In 1997 the NSF had twelve hundred employees and a budget of $3 billion a year. Attracting new scientists is no longer a problem; finding research jobs for them is. The NSF gets so many proposals from so many people that simply doing great work is no longer sufficient to ensure adequate, stable, long-term funding. Vannevar Bush’s system is straining under the weight of its own successful creation of an enormous academic research establishment.

It’s also struggling to cope with the consequences of the growth of the rest of the government. The original proposal for the National Research Foundation recognized that research is too unlike any other kind of government function to be managed in the same way; grantees would need the freedom to organize and administer themselves as they saw fit. The usual government bidding and accounting rules would have to be relaxed to encourage basic research.

Not that the government has been particularly successful at overseeing itself. The shocking inefficiency of the federal bureaucracy led to the passage in 1993 of the Government Performance and Results Act. GPRA sought to bring industrial standards of accountability to bear on the government, forcing agencies to develop clear strategic plans with measurable performance targets, and basing future budgetary obligations on the value delivered to the agencies’ customers.

This means that the U.S. government is now in the business of producing five-year plans with production targets, just as the former Soviet Union has given up on the idea as being hopelessly unrealistic. GPRA applies to the NSF, and its grantees, and so they must do the same. Therefore a basic research proposal now has to include annual milestones and measurable performance targets for the research. My industrial sponsors would never ask me to do that. If I could tell them exactly what I was going to deliver each year for the next five years then I wouldn’t be doing research, I would be doing development that they could better perform internally.

Vannevar Bush set out to protect research from the pressure to deliver practical applications, freeing it to go wherever the quest for knowledge leads. GPRA seeks to nail research to applications, asking to be told up front what a project is useful for. Both are good-faith attempts to derive practical benefits from research funding, and both miss the way that so much innovation really happens.

Vannevar Bush’s legacy was felt at Bell Labs when I was there before the breakup of the phone system in the 1980s. The building was split into two wings, with a neutral zone in the middle. Building 1 was where the basic research happened. This was where the best and the brightest went, the past and future Nobel laureates. The relevant indicator of performance was the number of articles in the prestigious physics journal that publishes short letters, a scientific kind of sound bite. Building 2 did development, an activity that was seen as less pure from over in Building 1. This didn’t lead to Nobel prizes or research letters. Conversely Building 1, viewed from Building 2, was seen as arrogant and out of touch with the world. The cafeteria was between the buildings, but the two camps generally stuck to their sides of the lunchroom. Meanwhile, the business units of the telephone company saw much of the whole enterprise as being remote from their concerns, and set up their own development organizations. Very few ideas ever made it from Building 1 to Building 2 to a product.

There were still plenty of successes to point to, the most famous being the invention of the transistor. But this happened in exactly the reverse direction. The impetus behind the discovery of the transistor was not curiosity-driven basic research, it was the need to replace unreliable vacuum tubes in amplifiers in the phone system. It was only after the transistor had been found that explaining how it worked presented a range of fundamental research questions that kept Building 1 employed for the next few decades.

Few scientific discoveries ever spring from free inquiry alone. Take the history of one of my favorite concepts, entropy. In the mid-1800s steam power was increasingly important as the engine of industrial progress, but there was very little understanding of the performance limits on a steam engine that could guide the development of more efficient ones. This practical problem led Rudolf Clausius in 1854 to introduce entropy, defined to be the change in heat flowing into or out of a system, divided by the temperature. He found that it always increases, with the increase approaching zero in a perfect engine. Here now was a useful test to see how much a particular engine might be improved. This study has grown into the modern subject of thermodynamics.

The utility of entropy prompted a quest to find a microscopic explanation for the macroscopic definition. This was provided by Ludwig Boltzmann in 1877 as the logarithm of the number of different configurations that a system can be in. By analyzing the possible ways to arrange the molecules in a gas, he was able to show that his definition matched Clausius’s. This theory provided the needed connection between the performance of a heat engine and the properties of the gas, but it also contained a disturbing loophole that Maxwell soon noticed.

An intelligent and devious little creature (which he called a demon) could judiciously open and close a tiny door between two sides of a box, thereby separating the hot from the cold gas molecules, which could then run an engine. Repeating this procedure would provide a perpetual-energy machine, a desirable if impossible outcome. Many people spent many years unsuccessfully trying to exorcise Maxwell’s demon. An important step came in 1929 when Leo Szilard reduced the problem to its essence with a single molecule that could be on either side of a partition. While he wasn’t able to solve the demon paradox, this introduced the notion of a “bit” of information.

Szilard’s one-bit analysis of Maxwell’s demon provided the inspiration for Claude Shannon’s theory of information in 1948. Just as the steam engine powered the Industrial Revolution, electronic communications was powering an information revolution. And just as finding the capacity of a steam engine was a matter of some industrial import, the growing demand for communications links required an understanding of how many messages could be sent through a wire. Thanks to Szilard, Shannon realized that entropy could measure the capacity of a telephone wire as well as an engine. He created a theory of information that could find the performance limit of a communications channel. His theory led to a remarkable conclusion: as long as the data rate is below this capacity, it is possible to communicate without any errors. This result more than any other is responsible for the perfect fidelity that we now take for granted in digital systems.

Maxwell’s demon survived until the 1960s, when Rolf Landauer at IBM related information theory back to its roots in thermodynamics and showed that the demon ceases to be a perpetual-motion machine when its brain is included in the accounting. As long as the demon never forgets its actions they can be undone; erasing its memory acts very much like the cycling of a piston in a steam engine. Rolf’s colleague Charles Bennett was able to extend this intriguing connection between thought and energy to computing, showing that it is possible to build a computer that in theory uses as little energy as you wish, as long as you are willing to wait long enough to get a correct answer.

Rolf and Charles’s work was seen as beautiful theory but remote from application until this decade, when power consumption suddenly became a very serious limit on computing. Supercomputers use so much power that it’s hard to keep them from melting; so many PCs are going into office buildings that the electrical systems cannot handle the load; and portable computers need to be recharged much too often. As with steam engines and communication links, entropy provided a way to measure the energy efficiency of a computer and guide optimizations. Lower-power chips are now being designed based on these principles.

This history touches on fundamental theory (the microscopic explanation of macroscopic behavior), practical applications (efficient engines), far-reaching implications (digital communications), and even the nature of human experience (the physical limits on thinking). Yet which part is basic, and which is applied? Which led to which? The question can’t be answered, and isn’t particularly relevant. The evolution of a good idea rarely honors these distinctions.

The presumed pathway from basic research to applications operates at least as often in the opposite direction. I found out how to make molecular quantum computers only by trying to solve the short-term challenge of making cheap chips. If I had been protected to pursue my basic research agenda I never would have gotten there. And the converse of the common academic assumption that short-term applications should be kept at a distance from basic research is the industrial expectation that long-term research is remote from short-term applications.

A newly minted product manager once told me that he had no need for research because he was only making consumer electronics, even though his group wanted to build a Global Positioning System (GPS) receiver into their product. GPS lets a portable device know exactly where it is in the world, so that for example a camera can keep track of where each picture was taken. It works by measuring the time it takes a signal to reach the receiver from a constellation of satellites. This requires synchronizing the clocks on all of the satellites to a billionth of a second. To measure time that precisely, each satellite uses an atomic clock that tells time by detecting the oscillation of an atom in a magnetic field. According to Einstein’s theory of relativity, time slows down as things move faster, and as gravity strengthens. These effects are usually far too small to see in ordinary experience, but GPS measures time so finely that the relativistic corrections are essential to its operation. So what looks like a simple consumer appliance depends on our knowledge of the laws governing both the very smallest and largest parts of the universe.

Across this divide between the short and long term, a battle is now being fought over the desirability of basic versus applied research. The doers of research feel that they’ve honored their part of the bargain, producing a steady stream of solid results from transistor radios to nuclear bombs, and cannot understand why the continuing funding is not forthcoming. The users of research results find that the research community is pursuing increasingly obscure topics removed from their needs, and question the value of further support.

As a result both academic and industrial research are now struggling for funding. Many of the problems that inspired the creation of the postwar research establishment have gone away. The most fundamental physics experiments have been the studies at giant particle accelerators of the smallest structure of matter; these were funded by the Department of Energy rather than the National Science Foundation for an interesting historical reason.

After World War II the researchers who developed the nuclear bomb were clearly of great strategic value for the country, but few wanted to keep working for the military. So Oppenheimer made a deal for the government to fund particle physics research to keep the community together and the skills active, with the understanding that it might be tapped as needed for future military needs. The Department of Energy then grew out of the Atomic Energy Agency, the postwar entity set up to deal with all things nuclear. Now with the end of the cold war the demand for nuclear weapons is not what it used to be. At the same time, the particle experiments have reached a scale that new accelerators can no longer be afforded by a single country, if not a whole planet. Further scientific progress cannot come easily the way it used to, by moving to ever-higher energies to reach ever-finer scales. So there are now a lot of high­energy physicists looking for work.

Similarly, the original success of the transistor posed many research questions about how to make them smaller, faster, quieter. These have largely been solved; an inexpensive child’s toy can now contain a chip with a million perfect transistors. There is still an army of physicists studying them, however, even though we understand just about everything there is to know about a transistor, and can make them do most everything we want them to.

What’s happened is that disciplines have come to be defined by their domain of application, rather than their mode of inquiry. The same equations govern how an electron moves in a transistor and in a person. Studying them requires the same instruments. Yet when my lab started investigating the latter, to make furniture that can see and shoes that can communicate, along with all of the interest I was also asked whether it was real physics. This is a strange question. I can answer it, dissecting out the physics piece from the broader project. But I don’t want to. I’d much rather be asked about what I learned, how it relates to what is known, and what its implications are.

Vannevar Bush’s research model dates back to an era of unlimited faith in industrial automation, and it is just as dated. Factories were once designed around an assembly line, starting from raw materials and sequentially adding components until the product was complete. More recently it’s been rediscovered that people, and machines, work better in flexible groups that can adapt to problems and opportunities without having to disrupt the work flow. Similarly, there is a sense in which a conveyor belt is thought to carry ideas from basic research to applied research to development to productization to manufacturing to marketing. The collision between bits and atoms is a disruption in this assembly line that cries out for a new way to organize inquiry.

Joe Paradiso turning an experiment into a magic trick, and Phil Rittmueller turning that into an auto safety product, provide a clue for where to look. A secret of how the Media Lab operates is traffic: there are three or four groups in the building every day. We’re doing demos incessantly. This never happens in academia, because it is seen as an inappropriate intrusion into free inquiry. And it’s not done in industry, where knowledge of internal projects is carefully limited to those with a need to know. Both sides divide a whole into pieces that add up to much less.

The companies can come in and tell us when we’ve done something useful, like the car seat. They can do that far better than we can. And, they can pose what they think are hard problems, which we may in fact know how to solve. Instead of writing grant proposals I see visitors, something that I would much rather do since I learn so much from them. After helping them with what I know now, I can use their support to work on problems that would be hard to justify to any kind of funding agency. Ted Adelson nicely captures this in a simple matrix:

Looks-easy-is-easy questions do not need research. Looks-hard-is-hard is the domain of grand challenges such as the space program that require enormous resources and very long-term commitments. Looks-hard-is-easy are the short-term problems that are easy to convey in a demo and to relate to an application. Looks-easy-is-hard are the elusive problems that really motivate us, like figuring out how machines can have common sense. It’s difficult to explain why and how we do them, and hence is hard to show them in a demo. The lower-left corner pays the bills for the upper right, openly stealing from the rich projects to pay for the poor ones.

The third trick that makes this work is the treatment of intellectual property, the patents and copyrights that result from research. Academia and industry both usually seek to control them to wring out the maximum revenue. But instead of giving one sponsor sole rights to the result of one project, our sponsors trade exclusivity for royalty-free rights to everything we do. This lets us and them work together without worrying about who owns what. It’s less of a sacrifice for us than it might sound, because very few inventions ever make much money from licensing intellectual property, but fights over intellectual property regularly make many people miserable. And it’s less of a sacrifice for the sponsors than it might sound, because they leverage their investment in any one area with all of the other work going on. When they first arrive they’re very concerned about protecting all of their secrets; once they notice that many of their secrets have preceded them and are already familiar to us, and that we can solve many of their internal problems, they relax and find that they get much more in return by being open.

The cost of their sponsorship is typically about the same for them as adding one new employee; there are very few people who can match the productivity of a building full of enthusiastic, unconstrained students, and it’s hard for the companies to find and hire those people. Any one thing we do the sponsors can do better if they really want to, because they can throw much greater resources at a problem. The difficult thing is figuring out where to put those resources. We can happily learn from failing on nine projects, something that would bankrupt a company, and then hand off the tenth that succeeds.

This relationship in turn depends on another trick. We have a floor of people who wear suits and write memos and generally act corporate. This is essential to translate between the two cultures. Most every day I see industrial visitors asking to fund physics research, even though they don’t realize that’s what they are saying. They’re posing problems without knowing where to look for solutions. It’s unrealistic to expect them to come in understanding what disciplines are relevant, and how to work with them.

Sponsors as well as students need training. I realized this when a company visited, was excited by what they saw and became a sponsor, and just as quickly terminated their support, explaining that we were not delivering products in a timely fashion. The real fault lay not with them for so completely missing what a research lab is for, but with us for not recognizing and correcting their misunderstanding.

Over time, I’ve come to find that I like to work equally well with Nobel laureate scientists, virtuosic musicians, and good product managers. They share a remarkably similar sensibility. They have a great passion to create, bring enormous discipline to the task, and have a finely honed sense of what is good and what is bad.

While their approaches overlap, their training and professional experience do not. Mastery of one helps little with another. Yet this is exactly what companies presume when they look to their researchers to find applications for their work. I was visiting a large technology company once that was trying to direct its research division to be more useful. They did this by setting up a meeting that was more like a religious revival, where researchers were asked to come forward and testify with product plans. Not surprisingly, the researchers didn’t have a clue. It takes an unusual combination of life experience and disposition to excel at perceiving market opportunities and relating them to research capabilities.

In between the successful scientist, artist, and manager is a broad middle ground where work does not answer to a research discipline, or a critical community, or the marketplace. Nicholas Negroponte and I spent a morning attending a research presentation at an industrial lab along with the company’s chain of command. After a laborious discussion of their method, exactly how they went about designing and evaluating their project, they finally showed what they did. Nicholas was livid—an undergraduate could (and in fact did) accomplish the same thing in a few afternoons. He couldn’t believe the waste of everyone’s time. Amid all their process they had forgotten to actually do something. Because the same group of people were posing the question, doing the research, and evaluating the results, that message never reached them.

This is one more reason why demos are so important. They provide a grounding that is taken for granted in a mature field but that otherwise would be lacking in an emerging area. A steady stream of visitors offers a reality check that can help catch both bad and good ideas. This is a stretch for corporate cultures based around carefully controlling access, a protective reaction that can cause more harm than good in rapidly changing fields. I’ve seen corporate research labs that require management approval even for Internet access, limiting it to those employees who can show a job-related need to communicate. This distinction makes about as much sense as asking which employees have a job-related need to breathe; not surprisingly it keeps out much more information than it lets in.

Demos serve one more essential function. Our students spend so much time telling people what they’re doing that they get good at communicating it to varied audiences, an essential skill lacking in most of science. And then eventually, after doing it long enough, they start to figure out for themselves what they’re really doing. One of my former students told me that he found this to be the single most important part of his education, giving him an unfair advantage in his new lab because none of his colleagues had experience talking to nonscientists about their work.

Too much research organization is a matter of constraints, trying to decide who should do what. The sensible alternative that is regularly overlooked is contact, trying to bring together problems and solutions. Since the obvious connections have long since been found, this entails finding the non-obvious ones like the car seat that would not show up on a project list. The only successful way I’ve ever seen to do this is through regular visits that allow each side to meet the other.

It is a simple message with enormous implications. The result in the Media Lab is something that is not quite either traditional academia or industry, but that draws on the best of both. This model is not universally applicable; some problems simply take lots of time and money to solve. But it sure is fun, and it lets us pursue ideas without trying to distinguish between hardware and software, content and representation, research and application. Surprisingly often, working this way lets all sides get exactly what they want while doing just what they wish.

The inconvenient technology that we live with reflects the inconvenient institutional divisions that we live with. To get rid of the former, we need to eliminate the latter.

WHEN THINGS START TO THINK by Neil Gershenfeld. ©1998 by Neil A. Gershenfeld. Reprinted by arrangement with Henry Holt and Company, LLC.