the list was not exhaustive:
Software Testing (finding and fixing bugs)
Internal Programming Tools (to improve the efficiency of programming and speed technology transfer)
New Programming Languages & the SQL Paradigm
Operating Systems Research
End-to-End Systems (integrating a range of technologies to solve user problems from end to end: as an example, he cited work from Xerox PARC aimed at creating the “paperless office.”)
Applications Research
I don’t know which of these efforts MSR actually pursued at the time, or how deeply it pursued them. It would be incredibly hard to sort out, even if Microsoft was willing to share the information.
But I would like to make two points. First, the list shows real awareness of what was needed—and is still needed—in software and computing. I, personally, am stunned that with all the brilliant research at Microsoft and many other companies and universities, we have not yet moved computing into a fundamentally new desktop operating system paradigm, i.e., something better than the graphical user interface that was pioneered at Xerox PARC back in the ‘70s. Even with mobile emerging as the new OS paradigm, the interface itself still depends heavily on icons, files, and even the keyboard.
The other thing that jumped out at me was the focus on software applications—especially given the way “apps” have taken off in recent years. As Myhrvold wrote, “Historically, most computer science research has been in one of two general classes—focused niche work that is about a very specific problem domain (speech, natural language, vision, graphics…) or systems work (operating systems, networking, database, programming languages…). End user applications have been underrepresented in both academic work and in most industrial research labs. The most famous exception is Xerox PARC, which invented paint programs, rich text word processors and many other important applications.
“We have followed this general trend for the most part…This situation is out of line with our priorities, given that applications are such a huge business for us. Research in both new kinds of applications and new ways to apply technology to application problems is very worthwhile.”
Myhrvold listed three initial examples of areas MSR could start applications research: natural language word processing, eliminating physical file cabinets, and what he called “object protocols for web Office.”
Again, it is very difficult to sort out exactly what happened as a result of this memo. But unfortunately for Microsoft, any research it did into applications does not seem to have had a major impact on its current product line, even as it competes in the mobile-cloud landscape.
Wild & Crazy Stuff (pp. 11-14)
The last section of the 12-page report was devoted to far-out areas. According to its original plan, Microsoft Research had been set up to focus on problems two to five years from potential commercialization. Now, Myhrvold asked if its research horizons should be expanded.
“Should we pursue very long term or highly speculative research?” he wrote. “When our research effort was smaller it was very easy to answer this—no. There was too much low hanging fruit to be had for us to spend time working on things that were farther out. That conservative line may still be our best policy, but given our new scale it’s at least worth considering whether there are bolder approaches that could be taken.”
You might expect Myhrvold, who has a PhD in theoretical and mathematical physics from Princeton University and worked under Stephen Hawking at the University of Cambridge on a post-doctoral fellowship, to whole-heartedly embrace the farther-out. However, he proved surprisingly reluctant to do so.
“One rationale that is often proposed for having diverse research agendas is unexpected benefits from cross fertilization. People may get inspired by something from physics or biology and have it lead to all sorts of benefits for software and computer science. This is the James Burke ‘Connections’ theory of progress. It certainly does occur, but not enough to justify staffing up research in all areas of science. If our people can get great ideas by talking to a biologist or physicist we should encourage it, but the biologist does not need to be on the payroll. They can be at UW [University of Washington] or nearly anywhere else. We can get most of the benefit of cross fertilization by allowing senior researchers to pursue a certain amount of interdisciplinary work as a side interest, collaborating with people in other institutions if need be.”
His bottom line: “when it comes to branching out beyond software, there is very little leverage for us.”
Myhrvold begins to wrap up the memo by noting, “This still leaves us with a lot of wild & crazy stuff. Here is an initial list.” And the rest of the memo consists mostly of his take on nine far-out, but potentially fundamental, areas of inquiry that might fit his criteria—many revolving around artificial intelligence or new forms of computing:
Artificial intelligence
Linguistic approach to AI
Brain modeling
Quantum computing
DNA computing
Artificial life & genetic programming
Software aspects of nanotechnology
Protein folding & molecular CAD
Computational economics
Myhrvold writes a paragraph or so of explanation for each of these areas—those summaries are quite revealing, so I encourage you to read them. As for choosing which of these to pursue, he sums up his approach as follows: “Deciding on exactly which topics depends a lot on our hiring opportunities. My enthusiasm for doing a very difficult problem depends primarily on whether we have found the key genius that seems capable of solving it. The next level priority for me is whether I can have confidence in the basic approach. Third, but still important, I would ask what synergy this has with products or other research, and what we’d do if we succeed. I’d find it rather embarrassing to hire brilliant people, beat the incredible odds, make a tremendous breakthrough—and then have no idea what to do next.”
His ultimate conclusion: “On this basis, if I had to make the decision right now (which I do not), I’d say that we should have a couple of ‘AI’ projects—one building on the linguistic work we have done, and perhaps one along the lines of brain modeling. We probably should do something in genetic programming, and also computation economics insofar as it relates to the net. I’d skip DNA computing (it’s a hardware or rather wetware issue), protein folding and nanotechnology. For Quantum computing I’d have some of our existing people keep tabs on it, but not start a dedicated effort at this point.” (This is a reference to the fact, as he points out in the memo, that a group of MSR cryptographers was already moonlighting in quantum computing.)
Ultimately, as far as I know, Microsoft Research did go into many of the areas Myhrvold outlined in some form or other, though I have not had time to determine their current status. I also can’t help but wonder, given the current climate and Nadella’s e-mail, how much of this sort of inquiry will continue in the future, although I know from speaking with current research director Peter Lee last year that maintaining a core of blue sky, far-out research was part of his plan.
For this article, though, let me end with a different question. Was Myhrvold on target with his own “wild & crazy” agenda items? I think you could say the same list might hold up extremely well today, some 17 years later.
