Expansion of Microsoft Research—Analysis and Download of 1997 Plan
“We are about to embark on a nearly unprecedented adventure—expanding Microsoft’s investment in research by at least a factor of three.“
So begins the May 1997 memo written by Nathan Myhrvold, architect of Microsoft Research (MSR), a little over five and a half years after the renowned research organization was created. The memo, labeled Microsoft Confidential, marked a new phase in the evolution of what has arguably become the world’s leading corporate research organization in software and computing—signaling its move from a one-off lab into the global organization it is today, boasting some 1,100 scientists and engineers in seven research labs and five other tech centers around the world.
The early MSR had tasted success, and it wanted more. As Myhrvold (he ultimately rose to chief strategist and CTO at Microsoft before founding Intellectual Ventures in Bellevue, WA) continued in the memo’s opening paragraph: “A few years [ago] some of us were fortunate enough (and naïve enough) to participate in the adventure of expanding our research by an infinite factor—from zero to something. That something has been incredibly successful, to the point that we now want to create something larger still.”
The 1997 memo (a PDF of the entire 14-page memo is below) can be seen as the sequel to Myhrvold’s 1990 memo and PowerPoint presentation that convinced Bill Gates and other Microsoft executives to create the research lab in the first place: the lab officially launched in September 1991 and will celebrate its 23rd anniversary this fall. (You can find a PDF of that 21-page 1990 memo here, along with my detailed analysis. And here is Myhrvold’s original presentation and my shorter analysis.)
I have been meaning to write this sequel for a while now. It has become even more top of mind, though, given the July 10 e-mail from new Microsoft CEO Satya Nadella to company employees. The memo emphasized the company’s business focus on mobile and the cloud. It referred to impending engineering and organizational changes—the company announced its biggest layoff in history on Thursday—and the imperative of innovation and “reinventing productivity.” But while Nadella cited many products and areas in which MSR has long been involved, he made no mention of the research organization itself or more basic research in any form. I don’t want to read too much into one communique. However, given some changes at MSR over the past year under new director Peter Lee to connect the organization better to business needs—changes sure to accelerate under the new CEO—it seems clear that overall time horizons of research projects are likely to shrink.
The opposite was being contemplated when Myhrvold wrote his 1997 memo. That is, while MSR had focused from day one on building ties to the company’s product groups, nearly six years into the effort Myhrvold felt the need to at least consider looking farther out and conducting more fundamental research. And while he ultimately rejected most of this idea, the lab did indeed expand its horizons in the years ahead (see last section for more on this).
We’ll dive into the memo to better understand how things have changed—but first some context. When he conceived of MSR back in 1990, Myhrvold headed Advanced Technology and Business Development for Microsoft and was just trying to get a small research lab off the ground. He proposed forming several research groups of five to 10 people each, growing to a total headcount of 30 in the first year, 50 during the second year, and 60 after three years. Among the very first hires was research director Rick Rashid, a star computer scientist from Carnegie Mellon University who would lead MSR until July of 2013, when he turned over the reins to Lee. (As part of the transition, Rashid, a senior vice president, joined Microsoft’s Operating Systems Engineering Group). Other initial recruits included minicomputer pioneer Gordon Bell, now a researcher emeritus at the organization, and three linguistic and natural language stars from IBM Research: Karen Jensen, Stephen Richardson, and George Heidorn.
I could find nothing in the original proposal that envisioned a much bigger organization—although, knowing Myhrvold, that must have been in his mind from the start. By 1997, in any case, he and Rashid had decided the time was right to make MSR much more of the hallmark research organization it is today.
I invite you to read the full memo for yourself. But below I have highlighted what I see as key parts of the document, and included some commentary that I hope is helpful in contemplating the evolution of Microsoft and its place in the annals of computing and software R&D.
Top 3 Goals (pp. 1-2)
While decrying mission statements, Myhrvold laid out three main goals of the planned expansion:
Create the premier software research institution in the world.
Invent the critical technologies to carry computing through the early 21st century.
Drive technology into Microsoft products, and help our company remain preeminent in its field.
“So, to be clear about it, I want to do all three,” he wrote. “I do not want to choose. I do not want to prioritize one over another. I believe that if we take the right approach they do not trade off against one another, but rather are reinforcing.”
As Myhrvold points out in the memo, these three goals are related but not necessarily dependent on each other. I would argue that MSR has done a great job with goals 1 and 3. (Yes, I know many outside “critics” have slammed the lab on the third point, saying MSR has not contributed its fair share to Microsoft businesses, but the cases of research benefitting Microsoft are legion and well documented, in products from Office to Bing to Xbox and Kinect and in areas such as speech, cloud, mobile, and more.)
However, I do feel it has come up short on goal 2. At least, I can’t name a truly major breakthrough or invention out of MSR—and while the lab lists many awards and influential papers on its website, I could not find any mention of anything seminal. That might be okay, though. As Myhrvold wrote in 1997, “You could create a great institution even if you don’t invent some of the most critical technologies. It is quite possible to putter along with our researchers earning back their salaries with benefit to the company, yet never having the big breakthrough.”
How to Add Headcount (pp. 2-3)
Myhrvold laid out a plan for massive expansion, but he was extremely wary about adding headcount to existing groups. For one thing, he worried that more personnel would tilt their focus toward moving things to product groups too early in their development—what he called “Newtonization,” after Apple’s Newton handwriting system, which proved a major failure when rushed into product. (The iPhone would have a much different result, of course. And given Nadella’s e-mail, I can’t help but wonder if today’s Microsoft might also feel differently.)
“Put bluntly, I want to be very parsimonious with headcount to existing groups. Projects that really need more resources should get them, but only if we have a strong sense that we get more benefit from increasing our bet there versus making some new bet,” Myhrvold wrote.
This was a key move—and very much follows the expansion of other great labs before it, including IBM Research and Bell Labs. For MSR to truly be world class, it had to expand into completely new areas. There is a lot more of Myhrvold’s reasoning in the memo. But the key for me is that he was saying expansion into tangential areas could be left to product groups or not done at all in most cases. Microsoft Research had to blaze some new trails.
Plan Bs (pp. 4-5)
Myhrvold devoted a section to what he called “Plan B Approaches,” namely the idea that research groups tackling critical problems such as speech recognition or natural language understanding should have a backup plan (see p. 4). In most MSR groups, he noted, one key path or class of methods had been chosen—and the organization probably needed to hedge some of those bets.
“There is no precise way to do this…However, we certainly can identify areas where the research field has N well established approaches and we are pursuing a smaller number. We need to own up to this challenge and decide what areas deserve a ‘plan B’ approach. It seems very unlikely that looking across all of research, we are lucky enough to have optimal choice in every area. Even if we are that lucky, we should be willing to buy some insurance. Ideally, we can do this by incorporating senior expertise within our existing groups, so that we get the best of both worlds. However, in cases where this is impractical we may need to set up parallel efforts pursuing different approaches.”
Myhrvold recognized the dangers of creating internal “cutthroat competition,” which could poison relations between groups. “On the other hand,” he wrote, “we can’t let the threat of this stop us from pursuing legitimate alternative research avenues.”
New Groups & Projects (pp. 5-11)
Most of the rest of the memo is devoted to Myhrvold’s strategy for expanding into new avenues of research. Below is a list of areas—the parens are mine—he singled out for investigation, while stressing 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.”)
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:
Linguistic approach to AI
Artificial life & genetic programming
Software aspects of nanotechnology
Protein folding & molecular CAD
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.