On a bright sunny morning in early October of 1961 I walked up to the entrance of Bell Labs in Murray Hill, New Jersey for my first day of work. Somewhere within these storied walls were the heroes whose works I had studied in graduate school. Here Claude Shannon had conceived information theory, Steve Rice had written his landmark paper on noise, John Pierce had outlined the philosophy of digital communications, and Shockley, Bardeen, and Brattain had invented the transistor. Nobel laureates walked the corridors. I felt proud to have the opportunity to join such a famous community of engineers and scientists. For anyone in the communications field, Bell Labs was the place to be. Of course, besides feeling proud, I felt scared and inadequate. Who was I, next to such as these?

All these years later, I still feel that way. Occasionally I have looked back with admiration, nostalgia, and wonder at the names in a tattered 1965 Bell Labs telephone directory. It seemed that every single person in the research department in those days was then or was later to become famous. Several won Nobel Prizes, some became presidents of universities, while others wrote influential textbooks or had their names indelibly associated with breakthroughs in science and technology. What a world it was! The best thing about the old Bell Labs was that whatever you needed to know about, there was a world-class expert right down the hall.

Playing Follow-the-Leader

Leadership in those days emanated from technical or scientific expertise and fame. These were the people who indirectly controlled scientific research, not just at Bell Labs but also in the United States and the world beyond. We followed their examples not because they exerted management control, but because we sought the measures of technological and scientific success and acclaim that they had achieved. In my career as a Member of Technical Staff at Bell Labs, no one ever gave me an explicit assignment. It was assumed that you were self-motivated and self-led, and if you didn’t succeed in this context, you found a different job.

My initial assignment was in the data theory department of a laboratory responsible for developing commercial modems. I had no premonition that one day everyone would have modems in their homes and that these modems would use extremely complex signal processing and be implemented on a single chip. I thought that modems would always be big, clunky things used exclusively by industry. I was working on the problem of how to adapt modems to automatically equalize the various channel characteristics that they would encounter on dial-up. I think I chose this problem because it was mathematically interesting.

One evening I was stopped at a red light while driving home and I suddenly saw a simple way to implement an adaptive equalizer that would be optimum under the criterion that I had in mind. I was so excited about my idea that I stayed up all night, waiting for the sun to rise so it would be ok to go to work and tell people about it. Looking back on this I realize that the most rewarding moments of my career have not been promotions or awards, but the exhilaration that comes from a genuine, novel technical idea. Unfortunately, I can count on the fingers of one hand the number of times that I have had such ideas.

Past Projects Revisited

Bell Labs was such a vast place that it took several years of continuous osmosis for me to get a larger picture of what was happening there. When thinking about leadership it is interesting to consider some of the more important projects ongoing at that time. One of the best known was the development of Picturephone, which was thought to represent the future of communications. The 6.3 MHz analog signal from the Picturephone was to be carried over three pairs of wires to a special switch adjunct in the central office. The whole system required a re-engineering of the existing telephone infrastructure, and it was a monumental engineering development. A few years later I took a special, in-house course on “Managing Innovation”. The example of the “perfect” development project that we studied was Picturephone.

Picturephone was exhibited at the New York World’s Fair in 1964, and visitors there could talk to people across the country at a similar exhibit in Disneyland. Arthur C. Clarke saw the Picturephone in a visit to Bell Labs and used it extensively in the famous movie, “2001: A Space Odyssey.” Executives in Bell Labs had prototype Picturephone service within the Labs itself. A decade or so later I had a Picturephone myself, but by that time I think I had the last one in the world – there was no one left to call.

I sometimes reflect on this project. At that time this project was praised for its engineering excellence, but what are we to make retrospectively of its dismal market failure? Certainly a lot of the blame can be attributed to poor marketing judgment, but I think it is also true that such a project could only have endured within a culture such as that which existed at Bell Labs in those days – a benevolent monopoly with a vision of how the future should be and motivated much more by engineering excellence than by economics and market feedback.

The anticipated widespread adoption of the Picturephone was going to require a lot of bandwidth in the telephone plant. Fortunately, the researchers at Bell Labs were working on the answer to that bandwidth demand – it was to be the millimeter waveguide system. Even today when I sometimes drive by the old Bell Labs facility in Crawford Hill, New Jersey I see the legacy of that project. The Crawford Hill building is long and linear, having been designed to house the straight, experimental pipe that carried the circularly-polarized millimeter wave signal that was to be primary means of transport for information in the future.

The waveguide carrier system was unceremoniously dropped almost the instant the news came that Corning had made an optical fiber with the benchmark attenuation of only 20 dB per km. It was fortunate that most researchers who had worked on the waveguide system were skilled in the kinds of analysis needed for studying optical propagation in a guided medium. Bell Labs, to its credit, converted immediately to optical phenomena. Still, I wonder about the initial judgment behind the millimeter waveguide project. This, to me, was a classic case of underestimating the potential of competing technologies.

I had a personal experience of this underestimation (which Clay Christiansen has called “The Innovator’s Dilemma”) a decade later when I led a research team assembling a prototype of a digital switch. At that time in the mid-70s the core switching fabric was analog and implemented with remreed relays – electrical contacts embedded in small glass vials that cost only pennies to manufacture. How could a digital implementation with transistors compete with this well-honed, analog technology? I remember giving a sales pitch for our research prototype to the executive who headed the development of the new central office switch, which again was to employ an analog fabric. “But look how much more expensive your digital switch is,” he said to me. My presentation was a failure, but so was the newly developed analog switch when competitors came out with digital implementations.

I think back on this as a personal failure to understand – truly understand and believe – Moore’s Law. I should have told that executive that within a few years transistor switches would cost less than a few cents apiece. Much, much less, as we now know! Yet still I think most of us fail to believe and appreciate the exponential progress promised by Moore’s Law. It just can’t continue, we tell ourselves. We’re still telling ourselves this.

The Giants of Technology

Not all of the projects at Bell Labs then were as doubtful as the Picturephone and millimeter waveguide. I remember being interviewed in my initial visit to Bell Labs by a young department head, John Mayo, (later to become president of Bell Labs) who was heading the development of the first digital carrier system, T-1. And over in the research area, John Pierce was championing the development of satellite communications. Pierce was extremely influential in getting government cooperation for the experiments with the Echo satellite. The first signals to a communications satellite were sent from that same Crawford Hill facility designed for millimeter waveguide experimentation.

John Pierce was the preeminent technical leader of that day. He was both brilliant and eccentric. He would be speaking to someone on the phone and hang up in the middle of his own sentence when he found that his mind was elsewhere. It was disconcerting to be talking with him in the halls when he would suddenly tune out and walk away while you were still talking to him. You could almost see the “click” in his head, like a human remote control. Of course, eccentricity wasn’t unique in those days to Pierce. Shannon rode a unicycle in the halls and juggled in his office.

Pierce was famous for helping Rudy Kompfner to bring the radar technology from England to the United States during the war. He wrote science fiction under the pseudonym, J.J. Coupling, and he had the distinction of coining the name “transistor”. He always had a vision of the future of communications, and he had the energy, influence, and dedication to implement his visions. His last such vision at Bell Labs was of a packet network, implemented with a hierarchy of circular data LANs. It is sometimes said that his failure to get this vision adopted played a part in his decision to leave Bell Labs for Cal Tech. I remember the last time I saw him in the halls at Bell Labs. I asked him what Bell Labs would do without him. He said to me, “It’s up to you now, Bob.” I remember thinking that this wasn’t going to work. Technical leaders like Pierce have disappeared from our midst.

In 1982 I was promoted to head the communications research division. I inherited the office of Arno Penzias, who left one memento in his office for me – a silvered plaque on the wall of an AT&T advertisement featuring Penzias that had appeared in national publications. “What does a Nobel Prize in physics have to do with your telephone?” was the headline of the ad. It went on to explain that the work on radio astronomy that had led to his Nobel Prize for the big bang involved work on low noise amplifiers that were also critical for long distance telephone transmission. I thought then that this rationalization was a stretch, and now, sadly, I think that Nobel Prizes in physics may not have much to do with economic success in the telecommunications business. And I think that is a terrible shame. Perhaps AT&T didn’t profit, but society certainly did.

Fading of the Golden Years

There were still some good years left for research in 1982, but the dark clouds were gathering on the horizon. The next year I found myself on the stand in federal court in Washington, DC before Judge Greene at the AT&T anti-trust trial trying to explain the importance of research at Bell Labs and our guiding religion of trying to create the best telephone network for the country irrespective of economic gain to the company itself. But the Bell System was about to be broken up, and the fate of Bell Labs research was of minor consequence in the context of the tectonic forces that had been brought to bear.

While I was nervously defending Bell Labs to Judge Greene, researchers in academia were bringing up nodes on the experimental ARPANET. In 1983 there were fewer than a thousand hosts. Some researchers at Bell Labs were involved in this or similar activities, but probably no one believed that one day this fledgling network would threaten to devour the entire world’s telecommunications infrastructure. Between the technological forces unleashed by the Internet and the competitive forces unleashed by the AT&T anti-trust trial, the research world that we knew in those “golden years” of the 1970s and 1980s was about to crumble.

Like my predecessors and peers at that time, I tried to manage research by staying tuned to the technological landscape outside the company and making decisions about resource allocation among research projects according to my judgments on importance and viability. At research staff meetings we would go around the table and each director of a research lab would have seven minutes to trumpet the latest achievement of his lab. I remember hearing at this forum for the first time of many inventions and discoveries that later became immensely important. But I don’t remember often hearing about how any particular invention was going to make profit for the company. Technological innovation and scientific discovery were what mattered.

When I look back at the research projects for which I had responsibility, I see a very mixed bag, as I think all research must inevitably be. The research on optical transmission was steadily fruitful, while research on wireless and computer networking at that time was less readily applicable. I signed a form granting permission to give our source code for UNIX to a group of graduate students at Berkeley, little realizing that this would lead to BSD Unix and Sun Microsystems. I created departments for research in robotics and neural networks, which were instant fashions at that time, but which dimmed later when reality collided with expectations and hype. I supported a young physicist, Steven Chu, who wanted to trap atoms within colliding laser beams. He said at the time that the work could lead to a Nobel Prize. Years later it did.

Leadership Today

When I run into old Bell Labs people, we always talk about those “golden years”. But how the world has changed! The kind of management and technical leadership that existed in the old Bell Labs has vanished from the corporate environment. Today’s technical managers are much more concerned with business value than those past technical giants. Perhaps this is the way it should be, and in any event it is useless to lament what has passed. The attributes that I look for in a leader today are fundamentally the same ones I always did. I look for someone that I can respect and trust. In the old days respect and trust had to do with technology; now I have a more global understanding of what those attributes involve. Still, I’m glad I had the environment that I did!

Robert Lucky