2 September 2018 by Richard

Golden Eggs & Better Telescopes

Alan Kay, inventing the modern world

You may not have heard of Alan Kay, but you’ve used his ideas. Kay is an American computer scientist who contributed major parts of some of the biggest ideas in human-computer systems, like graphical user interfaces. Kay and colleagues like Douglas Engelbart were part of the “golden age” of computer innovation, when teams of researchers got lots of support and freedom not only to solve defined problems but also to identify new ones.

They got to do science like others do art, without being tethered to the past and without having to make industrial promises. In Kay’s own words (read the full excepts here):

The “golden age” funding included a lot of funding for “problem finding” — which means the funders were not vetting specific proposals or funding “directed research”. The points of agreement were on a “vision of desired future states”, not goals or routes. An example of the vision was Licklider’s “The destiny of computers is to become interactive intellectual amplifiers for all humans, pervasively networked world-wide”. This vision does not state what the amplification is like or how you might be able to network everyone in the world.

The golden age funders gave the equivalent in today’s dollars of several million dollars a year for five years to about 20 principal investigators so they could set up groups (much of the fundamental creative work in computing requires 8 or more people working together).

That sounds very liberating, compared to the research environments in both universities and private industry. Kay has a nice metaphor for such environments:

I once gave a talk to Disney executives about “new ways to kill the geese that lay the golden eggs”. For example, set up deadlines and quotas for the eggs. Make the geese into managers. Make the geese go to meetings to justify their diet and day to day processes. Demand golden coins from the geese rather than eggs. Demand platinum rather than gold. Require that the geese make plans and explain just how they will make the eggs that will be laid. Etc.


The golden age is long over, and it never existed for most researchers. But a very similar system has existed here in Germany for about 100 years: The Max Planck Society (formerly the Kaiser Wilhelm Society). The Max Planck Society gives the equivalent of one to a few million dollars a year to allow individuals to run research groups. These groups continue until the director retires. These groups are not founded upon detailed research proposals in which all of the problems and solutions have been mapped out. Rather they are founded on demonstrated ability and a vision for a future state of human knowledge. Once a topic is mainstream, the Max Planck Society loses interest. And it is happy to take risks. The Max Planck Society is venture capital for basic research.

High impact publication

I’m lucky enough to be one of these people with the unspecified many dollars (actually euros) each year to spend on research. This is a lot of responsibility, especially since the criteria I want my work to be judged on are radically different than that of standard university research.

Some people think that what I should be doing is producing Nature and Science papers. More than one colleague has specifically asked me which “Science/Nature projects” I have planned. That is not what Max Planck Departments are for. High-profile publications may arise, but they should be side effects. We demand wisdom, not professional impact.

So instead of pursuing my own glamorous research agenda, I am pursuing a vision of a desired future state for the study of human adaptation.

Finding vs Understanding

I am an evolutionary anthropologist. The public pays me to study where people came from and how our origins illuminate where we are going.

My focus is behavioral adaptation. Humans are successful because we adjust and adapt our behavior to variable circumstances—we succeed by doing different things in different contexts, and many of the things we do are novel. We also develop behavioral and technological solutions that evolve over generations. This allows the complexity of our behavior to exceed what any one person could invent, or even understand. Human adaptation is, for the lack of a better word, cultural. I’ve written much more about this here [PDF] and more recently here [PDF].

Human adaptation, extreme and specialized

So how to study all of this? Unlike other sub-fields of evolutionary anthropology, it isn’t possible anymore to make progress through discovery alone. In paleoanthropology, for example, the biggest news last year was the discovery of a modern human fossil dated at 300,000 years ago. In another department in my institute, they study ancient genomes, which has in recent years revealed surprising details about the evolutionary history of our species. Of course discovery-driven fields have the problem of chasing noise—new theories vastly overfit every new piece evidence. But they remain exciting and profitable, despite this.

In my sub-field, no one is going to discover a new society or behavior that will have much impact on theories of human adaptation. There was a time, last century, when the charting of human behavioral variation, including linguistic variation, produced many surprising discoveries. Most theories have accommodated (or denied) this evidence by now. There are still some discoveries to be made, for sure. But ratio has shifted. Now we’re in the long, hard slog of understanding. It hurts.

It hurts so badly, because experiment has a limited role to play. Why? The processes we are trying to study cannot be studied in the lab. Bits can be probed in the lab, for sure. I do experiments myself. Some of my best friends conduct experiments! But human adaptation is a long-term dynamic. It takes years for individuals to acquire adult competencies and generations for groups to adjust to changes in circumstance. Piecing together how life history, sociality, and cognition integrate in this process requires long-term, micro-level data, as well as a formal body of theory that can assemble such data into evidence.

Under the status quo, with short grants and institutional pressure to produce a steady stream of shallow publications, it’s very hard to make progress. Human adaptation takes place on a timescale that exceeds the typical academic career. It certainly exceeds the typical grant duration.

Not all anthropologists are going to lay golden eggs. But in the current system, none of them will.

The public is not getting a lot for its money. Look—I’m a military kid. Both of my parents were soldiers during the Cold War. I was weaned on public service and civic duty. If the tax payer is being cheated, it makes me viscerally upset. I am not upset at individuals, but rather at the system. I am broadly upset at science, and specifically upset at my own field.

A Better Telescope

Hubble images, before (top) & after (bottom) the camera was fixed

So instead of pursuing my own glamorous research agenda, I am pursuing a long-term infrastructure project. The infrastructure I have in mind is organizational and cultural, not narrowly technological. We must build a better telescope, one that can see the process of human adaptation at the time scale it happens and in the environments it happens in.

Consider the Hubble Space Telescope. When the Hubble went into orbit in 1990, it had a defective camera. It was a joke, a waste of public funds. But when the images started coming in, it turned out to be not so funny—despite being broken, the Hubble produced better images than any ground-based telescope to date. What the Hubble saw transformed astronomy. Once the camera was fixed, in 1993, images were even better (see right). But the point is that it didn’t have to be perfect to constitute a major advance.

The study of human adaptation needs a similar instrumentation advance. We are trying to study and theorize about a process we cannot see. And we are trying to do it by cobbling together short-term funding that has to promise transformative results. It would be funny, but it’s not.

I don’t exactly know how to accomplish this. But I am going to try, and I am confident that whatever we build will, at first, be broken. But it will still be better than any ground-based telescope.


How can we do better? I have a lot more to say, especially about professional norms and standards of training. I will write more about that in the future.