Don’t schedule breakthroughs

Most technology we see and handle everyday has a connection to inventors at Bell Labs, which was the center of post-war innovation nationally and globally. Comment # 13 on this link is from a former Bell Labs researcher, John Mashey. (The link itself is about the Integral Fast Reactor, a possible energy system that could help replace coal plants around the world). The comment is really interesting and useful, not just about technology but development and problem-solving in general — so I just copied and pasted it here.

John Mashey said

3 December 2008 at 16.20


Once upon a time, Bell Laboratories employed about 25,000 people in R&D, and was usually considered the premier industrial R&D lab in the world, for many decades. To be a Member of Technical Staff, one needed an M.S. or PhD. It was part of the Bell System, about which one can say “monopoly money is really nice.”

From its creation in 1925 onwards, Bell Labs generated:

– a few Nobel prizes
– numerous important breakthroughs
– a truly huge number of incremental improvements

See Bell Labs History, and see their pick of top 10 innovations. Modern technology has many other contributors, but an amazing amount of modern computing and communications technologies has some heritage somewhere in Bell Labs’ patents, software, or mathematics.

For example, if you use UNIX, Linux, MacOS, or even Windows, you use some features that originated in UNIX in the 1970s, and if you use the Internet, your packets are being handled by CPUs designed more for C than anything else.

I worked there from 1973-1983, fortunately mostly within excellent management chains and for many outstanding managers, including one who became CTO of Bell Labs and another who became President. Bell Labs generated many breakthroughs, BUT:

These managers always said:

“Never schedule breakthroughs.”

Why would they say that? And if great managers at a premier R&D lab didn’t think they could do it, should that be a caution?

Consider normal good R&D portfolio management, as practiced by companies and governments capable of long-term thinking, and who understand technology diffusion and inertia of huge installed bases.

Our classification was more-or-less as follows, although different people use different labels, and in some places, combine R2+D1, or D1+D2, or R2+D1+D2
I’ve never managed R1, have done/managed the rest:

Pure Research (R1) many little projects, modest $
Applied Research (R2)
Exploratory Development (D1)
Advanced Development (D2)
Development (D3) might include pilot plants, beta tests, etc.
Deployment & scaleup, cost reductions, etc. (D4) $$$$$$

The typical methodology is:

a) Spend a big chunk of $$ on deployment of what works already, knowing that volume & experience will help costs come down, and of course, in the energy case, there are plenty of efficiencies around that are zero-cost, although they may require upfront capital.

b) Meanwhile, spend some money on lots of little Research projects, select ones that have promise and take them further. This is usually called “progressive commitment”, i.e., you normally have lots of little R projects, and fewer, but bigger D projects, and then most of the money gets spent in deployment and scaleup of something you know works and can be scaled.

This avoids the common “MIT graduate student syndrome”:

Q: What can you build with 6 MIT PhD students?

A: Anything! ….
But you might only be able to build one of it…

c) One needs competent management of this process.

At Bell Labs, real R was only about 7%. Of course, that was tiny compared to the 100s of thousands of people involved in manufacturing, deployment, and support, and even small compared to the bulk of people doing Development.

The Bell System had more than 1M employees at that point, and really did think in terms of decades, which many businesses do not. The telephone network had some similarities with the power grid. Tiny efficiencies mattered. I recall a guy getting an award for saving a tiny fraction of the amount of gold needed for electrical contacts … but that was $Ms/year savings.]

Given the scale (in the old Bell System days), we had to install things that worked, not counting on what our R folks might invent. We knew they’d invent interesting things, but we also knew it might be *20 years* before we could really use them, and some things (like bubble memories) worked, but never well enough to win.

Some things were deemed interesting, but really niche, when first done … like lasers, or solar cells. Of course, while lasers have many surprise uses, one of the most importnat is running the fibreoptic links that carry most of the world’s communications traffic.

I know of two $B projects where they charged into fullscale Development too early, and wasted most of that money.

But, breakthroughs aren’t just accidents (Nassim Nicholas Taleb’s Black Swans to the contrary – his books have much merit, but when he gets into R&D management, I think he’s out of his turf, and he certainly says some wrong things about specific people I know well.)

If you want to get things to happen, you set up disciplined R&D programs that allow for the somewhat chaotic nature of real R1. Bell Labs invested in the smartest people we could hire, supported them superbly, picked people working in areas likely to be relevant, gave them long term timeframes, and had management support for capitalizing on their findings and diffusing technology appropriately and *commercially*.

[That was one of my explicit assignments for years: keep in touch with researchers, see if they’d invented anything that could be further productized, and mention real problems to them in the hopes that they might get interested. Sometimes they did.]

Note that this is different from building things (like the Manhattan Project] where cost is essentially no object. One may note that even in the USA, many military projects that once seemed budget-unlimited turned as much as they could to COTS (Commercial-off-the-shelf) rather than hand-built-specials.

THESE DAYS, Bell Labs is a much smaller place, XEROX PARC isn’t what it was, and in general, large industrial R&D is less prevalent. Government R&D labs range from superb to rather slow, and sometimes cost-insensitive. DARPA did some awesomely good project management.

In the USA, most R (R1 + R2) is done at universities, with government and/or industrial funding. Places like Stanford, Berkeley, MIT, Georgia Tech, etc, etc have serious efforts in many areas of energy R&D. See the GCEP program for example.

a) One needs the right project managers in government.

b) Good R&D must happen in universities and elsewhere.

c) then, it has to get commercialized, which may happen through existing companies or maybe startups. I work with VCs. They don’t fund R, at least not on purpose :-). They love D3 and D4, although they might fund D2 if they must, to get in early.

d) Government doesn’t simulate VCs very well, with rare exceptions. I’ve had to tell a number of government people that, and they never like to hear it. Government must fund basic research, pass the right rules, encourage entrepreneurs, make it easy to start and stop businesses, offer sensible consistency for long-term investments, etc.

Government’s role seems mainly in funding R1+R2, and enabling D4, and sometimes helping D3 with purchasing power. But in picking the potential winners in the middle, it is rare to find the right skill-set in government.


I’ll happily listen to people advocating massive R&D for energy projects, IF:

1) They explain the starting portfolio, including what stage each of the proposed projects is at, any known barriers, risks, scaleup issues, costs, etc. [Obviously more is known on some project that’s further along.]

Even while being a techno-optimist living in the very heart of techno-optimism, I tend to want to be careful about new ideas, because simple descriptions don’t really explain how far along such things really are.

2) They explain the R&D portfolio management strategy and who’s going to run it.

Energy stuff is *harder* than what we did at BTL, since Laws of Thermodynamics != Moore’s Law.
Anyway, whenever anyone says “R&D” or Research I try to ask them what they mean by that, because different people mean very, very different things. Just throwing money at the problem is *not* a good idea, without good management of the process.

4th generation nuclear may be a good idea, especially if it can burn up the radioactive junk that’s around. By law in CA, there will be no new nuclear reactors until the disposal problem is solved, and the history is not encouraging so far. But, I sure hope there’s a disciplined R&D plan that could yield at most a few standardized designs to replicate. However, we certainly can’t wait for it, although good nuclear plants do have the great advantage of being concentrated, in the same way coal/gas plants are, but unlike wind-turbines, so they can re-use existing grid layouts easily. Of course, the nice thing about wind turbines and CSP is that the technical risk is ~zero.


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