There’s a subtle distinction between freedom to suggest ideas and freedom to pursue ideas

# §Bell Labs Model

### Questions
- [[Why was Bell Labs Different?]]
- [[Why hasn’t Bell Labs been replicated?]]
- [[Was Bell Labs an anomaly?]]

### Conclusions
- [[Bell Labs and AT&T had timescale alignment]]
- [[Bell Labs is one of the few examples of an innovation org that was aligned with its money factory]]
- [[Bell labs had a budget of 2.8 billion 2020 dollars]]
- [[Bell Labs was only profitable in conjunction with AT+T]]
- [[AT+T benefitted significantly from creating better technology]]
- [[Regulation drove many of Bell Labs’ actions]]
- [[All the work at Bell Labs needed to tie back to the system]]
- [[Bell Labs empowered young people]]
- [[Bell Labs hired people before they had a role or expertise]]
- [[The work at Bell Labs that was most valuable to AT+T and the work that was most valuable to the world was fairly disjoint]]
- [[The famed bell labs research was a fraction of their activity]]
	- [[Bell labs was primarily not researchers]]
- [[Bell labs brought many disciplines together under the same roof and broke down barriers between them]]
- [[Bell Labs did not give researchers complete freedom]]
- [[Bell labs asked people to do useful things but left them room to say huh that’s funny]]
-  [[Bell Labs management was extremely light]]
- [[Bell Labs didn’t have a unique model]]
- [[Bell Labs selected for people with only academic pedigrees and with a sense of adventure]]
- [[Bell Labs was not a business]]::NW::
- [[Bell labs existed before continuous improvement was expected]] ::NW - stub::
- [[Bell Labs was a dance of individuals and institution, prototyping and manufacturing, invention and discovery]]::NW::
- - [[Bell Labs enabled free radicals]]



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Bell Labs

gertnerIdeaFactoryBell2012

Bell Labs management was extremely light

Regulation drove many of Bell Labs’ actions

Bell labs asked people to do useful things but left them room to say huh that’s funny

All the work at Bell Labs needed to tie back to the system

§Bell Labs Model

Labs Document Outline

# Bell Labs did not give researchers complete freedom
While [[Bell Labs didn’t have a unique model]] gave researchers a ton of leeway, they weren’t given complete freedom. Instead, they were generally given high level directions that would potentially be useful to AT&T - “figure out how to get more information in this copper wire” “figure out how to make switching speeds faster and more automatic” and *then* given freedom. They also just biased towards hiring people whose research interest lay in areas that seemed vaguely useful to AT&T.  Remember, [[AT+T benefitted significantly from creating better technology]].

All the stories of great bell outputs do seem to start with “so I was working on this practical high level directive.” However, unlike most goal-directed research now, it *does* seem like researchers were given the freedom to pursue tangent research based on ‘huh that’s funny moments’ like  [[The ability to say ‘huh that’s funny’ is important for discovering new phenomena]]. 

There’s a strain of thought that says “researchers should be given complete freedom to investigate what they want” independent of any consideration of use. This line of thinking is the main theme of [[brabenScientificFreedomElixir2008]] for example. It’s important to call out that this is not what Bell Labs did because in conjunction with Braben’s arguments the contrast suggests that both approaches can lead to paradigm-shifting discoveries. To use the [[Quadrant Model of Scientific Research]], Bell Labs operated from Pasteur’s Quadrant. The subtlety is that while they *started* with a consideration of use, sometimes it ended up with currently-useless fundamental understanding (like [[Cosmic Microwave Background]].) 

 Like many things, I suspect that hybridizing the two approaches will lead to failure. An organization needs to pick an approach and commit to it. 

### Related
- [[Einstein would have been stuck in a patent office - failures of paradigm-shifting science]]
- [[Venkatesh Narayanamurti Podcast 20 May 2020]]
- [[Andrew Odlyzko Podcast]]
- The freedom to pursue ‘huh that’s funny’ seems important for [[Possible FRO Structures]]

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Ideally corporate R+D enables work on a general purpose technology before it’s specialized

Ideally corporate R+D enables targeted dicking around

DeepMind combines bottom-up research work with top-down strike teams

One function of a private ARPA is to fill in the gap once filled by corporate R+D

Week of 29 Nov 2020

# Bell Labs enabled free radicals
[[Bell Labs]] narratives consistently touch on the theme of many very smart individuals who could attach themselves to different projects. In chemistry, free radicals are molecules with unpaired valence electrons - a state which makes them extremely reactive. The idea of free radicals captures a *feeling* one gets about Bell Labs that people were not on a project all the time, or at least had the bandwidth to engage with various projects they weren’t assigned to. There is also a sense that people also had a degree of autonomy over which projects they worked on. 

From [[gertnerIdeaFactoryBell2012]] - `”The Solar cell just sort of happened,” he [Cal Fuller] said. It was not “team research” in the traditional sense, but it was made possible “because the Labs policy did not require us to get the permission of our bosses to cooperate—at the Laboratories one could go directly to the person who could help.”`[[Bell Labs management was extremely light]]

Bell labs also used both culture and architecture to enable free radicals. It’s almost a trope now, but Bell Labs may have been the origin of the building design that maximized interactions. Bell Labs had high quality seminars starting in the 30’s that got people from different projects in a room talking about ideas. Culture and architecture combined in the practice of people always leaving their office door open so someone could come by and ask questions. [^1] [[Architecture matters for creativity]]. 

Of course, this isn’t to say that people just worked on whatever they wanted. [[Bell labs asked people to do useful things but left them room to say huh that’s funny]] so the freedom was usually within the scope of an area that would be useful to AT&T. Luckily that was a lot of areas. It’s also unclear how much this applied to the majority of Bell labs that was working on more direct product development instead of research and then how much that (less credited) group was responsible for Bell Labs’ perceived success. [[The famed bell labs research was a fraction of their activity]]. 

Enabling free radicals is line with how [[JCR Licklider]] managed the IPTO but stands in *contrast* to many other [[DARPA and corporate R&D filled overlapping but different niches]] programs. However, DARPA is actually woven *into* the US innovation ecosystem.  The fact that[[DARPA doesn’t do any research in house]] means that it cannot exist separately from [[aroraChangingStructureAmerican2020]].  It also means that any DARPA technologies cannot be attributed solely to DARPA, especially if they succeed. One must also consider the fact that program initiation is a spectrum from complete PM initiation to complete performer initiation. My hunch is that programs on the performer end of the spectrum had a chance to ramp up in a corporate lab.

### Related
- [[Bell Labs selected for people with only academic pedigrees and with a sense of adventure]]
- [[Designed Serendipity]]

[^1]: I suspect that open door policies are subtle and differ from open office plans. An open door says “I am in my own space and welcome you to come in — be considerate” while an open office says “I am at your disposal constantly without thinking.”



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Research requires more trust than other disciplines

For a certain class of research, deliverables can be detrimental

Bell labs brought many disciplines together under the same roof and broke down barriers between them

Bell Labs enabled free radicals

Bell Labs empowered young people

Comparing and contrasting Bell labs, DARPA, and Venture Research

# Bell Labs management was extremely light
Bell Labs management gave researchers autonomy, both to work on what they thought was best and with whom they wanted. While on paper this is what most management claims to do, in practice that’s rarely the case. So it’s worth digging into what light management at Bell Labs tactically entailed and perhaps how they were able to walk the walk instead of talk the talk. 

![](../BearImages/FBB01D7F-FB72-4B5D-A54A-87F6D9F98C8A-88049-0007B3CAFC68AFC1/IMG_0206.jpg)
Bell Labs had explicit policies that prevented managers from controlling who could collaborate with whom. My hunch is that the policies were more a codification of culture than anything else and someone citing the policy and telling their boss ‘you can’t stop me!’ was rare. However, it’s telling that unrestricted collaboration was part of the culture worth encoding. This managerial getting out of the way was one of the ways that [[Bell Labs enabled free radicals]]. 

![](../BearImages/358508FB-EFA0-44E8-997D-0CE7B250A8CA-88049-0007B3C5E0753C7D/IMG_0158.jpg)
`A believer in granting a degree of autonomy to researchers, he had not asked about, and had not been kept appraised of Bardeen and Brattain’s work. What’s more, there was a tendency at Bell Labs to confine important developments to middle management for a purgatorial period.`  
Bell Labs management did not put pressure on researchers to produce demos and there was an explicit time delay built in as the demos moved up the management chain. This approach — basically the inverse of the [[Media Lab]]’s “demo or die” — is worth calling out because expectations around demos have a strong effect on organizations that isn’t discussed enough. In some ways demos are valuable because they put pressure on people to get their work into a form that’s legible to people outside of their thought bubble. On the other hand they can often lead to creating “movie set products” where they are basically shiny shells that can do the demo and nothing else. Bell Labs’ management seems to have walked that line well. In order for the purgatorial period to work, moreover, the middle managers need to have in turn not felt pressure to surface demos in order to advance their careers. 

[[John Pierce gave four reasons why Bell Labs worked]] and `A technically competent management all the way to the top` is the first item on that list. I suspect that the technical competence helped the management stay light because it enabled trust between the managers and researchers. [[Research requires more trust than other disciplines]]. This trust meant that there was less dependence on metrics and milestones. The trust, and its resulting light management and efficiency is why [[People who have done a thing should be in charge of a thing]]. 

Interestingly, the management style at Bell Labs actually seems similar to [[JCR Licklider]]’s management at ARPA - find awesome people, get on the same page about the precise problems they’ll go after, and then let them rip. [[DARPA does multiple levels of top-down problem generation and bottom-up solution generation]]. 

At the same time, we shouldn’t hero-worship Bell Management.  Pierce may also have just been a bad manager and light management just kept him from doing damage….
`The brunt of his management work [at Bell Labs] had consisted of dropping in, unannounced, on colleagues in their labs to ask how work was progressing.`
![](../BearImages/A9B10EF2-FDC0-4C59-BA09-8A12263E8E2E-88049-0007B5D6B1243317/IMG_0253.jpg)

They still committed classic management false negative (preventing someone from doing something useful.) [[Types of management error]]. [[Gordon Teal]] still had to do the classic “work overnight on the side project” move to show that he actually could create high-purity chunks of germanium. ![](../BearImages/D5380E7F-E486-4A6B-991D-ECC088E27D58-88049-0007B4AFC620D39D/IMG_0169.jpg)

And of course, one has to hold the simultaneous views that while Bell Labs’ management was light, [[Bell Labs did not give researchers complete freedom]].  [[All the work at Bell Labs needed to tie back to the system]]. My current mental model for integrating these seemingly contradictory is similar to a coconut - high-resistance exterior and low resistance interior. [[Bell labs asked people to do useful things but left them room to say huh that’s funny]]. 

### Related
- [[Venkatesh Narayanamurti Podcast 20 May 2020]]
- [[odlyzkoDeclineUnfetteredResearch1995]]
- [[Andrew Odlyzko Podcast]]



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# Bell labs asked people to do useful things but left them room to say huh that’s funny
[[Bell Labs did not give researchers complete freedom]], however they also didn’t stop people from exploring if they discovered something that made them say “huh that’s funny.” [[The ability to say ‘huh that’s funny’ is important for discovering new phenomena]].  I suspect this mix of direction-setting led to results that wouldn’t happen either through pure bottom-up idea generation or focused top-down management.[[When is push or pull appropriate for innovation orgs?]].

The discovery of the [[Cosmic Microwave Background]] is of course, the exemplar of this operational mode. Penzias and Wilson were originally tasked to do something useful (experiments for satellite communications)  but had the bandwidth to run to (back)ground the reason for the persistent noise they picked up. It’s easy to imagine that on one hand, they might not even have been pointing the telescope at empty space if they weren’t working on the larger satellite system. (As trained astronomers I assume they would be looking at something more interesting.)  On the other hand, if they were under extreme pressure to get the project done or publish a paper about satellite communications they could easily have written off the noise as problematic equipment. 

This balance between pressure and [[Slack - concept]] resembles how [[DARPA does multiple levels of top-down problem generation and bottom-up solution generation]], both between directors and PMs and then between PMs and performers. The similarity suggests that that it might be an effective framework for approaching Pasteur’s Quadrant ([[Quadrant Model of Scientific Research]])  in a way that can enable Bohr’s quadrant type discoveries. 

There are a couple tactical upshots for innovation organizations in general. One is the fact that light management ([[Bell Labs management was extremely light]])  is actually structural. Another is that a major role for people higher in the hierarchy is to make problems as legible and precise as possible. Legible problems both shove people out of a comfort zone but give them the room to discover the unexpected. [[Legibility enables action]] 

### Related
- [[Why is there so little slack in mission-focused research?]]
- [[Bell Labs didn’t have a unique model]]
- [[Why hasn’t Bell Labs been replicated?]]


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The ability to say ‘huh that’s funny’ is important for discovering new phenomena

Bell Labs did not give researchers complete freedom

# Cosmic Microwave Background
[[Arno Penzias]] and [[Robert Woodrow Wilson]] were using the Holmdel Horn Antenna to try to do satellite communication experiments but noticed persistent noise in their measurements. Eventually they got in touch with theorists who pointed out this was predicted.

[[Serendipity]]
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IARPA

The best DARPA program managers are the ones who can look at an entire literature in an area and notice a systemic bias

§ARPA model

Heilmeier — Licklider — Braben — Elon quadrants of Research Management

DARPA Program managers pull control and risk away from both researchers and directors

What are the different roles in an innovation org?

Bartlett Russell

Data-Driven Discovery of Models (D3M)

riconFundPeopleNot2020

How does DARPA strike a balance between problem-focus and solution focus?

Defense Science Office - DSO

The coronavirus could lead to new institutional structures for long term preparation for tail events

Mihai Surdeanu conversation 14/2/20

World Modelers

Magnetically Actuated Micro-Robots for Advanced Manipulation Applications

# DARPA does multiple levels of top-down problem generation and bottom-up solution generation
In some ways the the Program manager is the ‘bottom up’ half of [[Top down problems and bottom up solutions]].  When DARPA hires someone, they are usually looking for someone to go after a vague area or problem rather than just hiring someone to fill a slot or because they’re great. So the DARPA director or previous program manager do a first pass of ‘top down.’  
The Program manager then synthesizes a program by digging into the current state of the discipline, what people on the bleeding think might be possible, and  integrating that with an idea of where they see the world going.  From the directors point of view this whole process is very bottom up. 

In other ways the program manager is the ‘top down’ half of [[Top down problems and bottom up solutions]]. When they are doing initial program design  ([[The DARPA execution framework boils down to showing that thing is not impossible, showing that thing is possible, and then making that thing possible]]) they talk to tons of researchers about possible directions and solutions. [[A large part of a DARPA program manager’s job is focused network building]]. During the actual execution phase, while PMs have a plan and an idea of who they want to deliver on it, they still put out a broad call that anybody can respond to at least nominally keep the door open to other bottom up solutions. 

In order to be a nexus of top-down and bottom-up approaches [[DARPA PMs need to think for themselves, be curious, and have low ego]]. If they don’t think for themselves, they will be at the whim of either the perceived desires of the director or the scientific community. If they’re not curious, they won’t actually synthesize anything interesting ([[The best DARPA program managers are the ones who can look at an entire literature in an area and notice a systemic bias]]) and will leave gems sitting by the roadside. Finally, if they don’t have low ego, they will build a program purely from their own ideas and cut off the bottom-up value of the system. 

### Related
- [[DARPA Program managers pull control and risk away from both researchers and directors]]

## References
- 
- 


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Bottlenecks Workshop June 2021

What does it mean for a research ecosystem to be healthy?

Healthy R+D orgs feel like they have very smooth project rampups with high ceilings

In the past, corporate labs filled a particular niche in the innovation ecosystem

Could FROs fill the gap left by corporate R+D?

ICT Distillation

26 Oct 2020

An Institute for Creative Technology - Riffing on ARPA

ICT Outline

# Ideally corporate R+D enables targeted dicking around
You have lots of stories of golden age R&D orgs where they’re literally just trying out a lot of stuff. “Hey, we came up with this new chemical, what’s it useful for?” In the startup world, that’s often derided as a “solution looking for a problem.” Arguably though, many important technologies started off this way - they weren’t a hole-in one solution to a problem. We don’t seem to have a place for this targeted dicking around to happen anymore for situations that require specialized knowledge and equipment.  

It’s important to call attention to the “targeted” part of “targeted dicking around.” Contrary to common perception, Bell Labs and PARC *didn’t* give researchers free rein to work on whatever they wanted.  There were relatively few milestones and researchers had enough slack from management to explore adjacencies. However, people were explicitly asked to work on high level goals that would benefit [[“The System” of AT&T]].

It’s almost impossible to confirm, but my hunch is that researchers who portray themselves as having free rein ([[Alan Kay]] comes to mind) are unreliable narrators. My hunch is that they perceive themselves as having free rein because the lab managers were good at hiring people whose interests were sufficiently aligned with the lab’s target that anything they chose to do was within some window. Another alternative is that they gave a *few* people free rein and the personal accounts are from the wunderkinds. [[The famed bell labs research was a fraction of their activity]]

[[Comparing and contrasting Bell labs, DARPA, and Venture Research]]

Disciplines where targeted dicking around can happen seem to be more healthy. You still see it a lot in software. It seems like there is a tradeoff between the democratization of a technology and the ability to dick around with it. Corporate R&D labs may have been able to change that equation. Stories about heyday chemical and other company R&D that created physical products - [[Nylon]], [[3M]] involved a lot of just ‘trying stuff out.’ It’s unclear that happens anymore 

There’s an implicit assumption that targeted dicking around happens in universities. This may be the case with *ideas* but it’s less so with technology applications. You can’t really write a paper about how you spent a year modifying your novel technology to 100 specific applications. 

Making a general purpose technology requires both generality and specificity. Great results have come from both a mode where people grope towards a general goal and also a mode where they grope towards a specific one. The development of the GUI at  [[Xerox PARC]] is a good example of the former mode. The PARC folks created general paradigms for computing like overlapping windows and visual representations of files that continue to dominate today by doing the hard work to build a full system, using it themselves, and seeing what worked. [[Edison’s Lab]] also did a lot of “trying stuff out” but in contrast to the taste-based cycles at PARC, the inventors at Menlo Park had a concrete application like a long-lasting-lightbulb in mind went through a thousand materials to see if they would fit the bill. This ‘iterating towards a concrete target’ mode of experimentation is much more suitable for startups. 

However, the two modes seem like they could be strongly coupled. While you’re trying out a thousand things to do a specific thing, you may realize that the five hundred and twenty first thing is no good for the intended purpose, but might be amazing at another thing. [[The ability to say ‘huh that’s funny’ is important for discovering new phenomena]]. However, that realization can easily be tossed out the door without the room to explore that hunch (because usually it’s a hunch.) Startups, academia, and 21st century R&D are rarely set up incentive-wise to enable to run that hunch to ground. You *do* see this happen with software startups because it is *much* easier to do targeted dicking around with software. Arguably this could be one reason that we’ve seen less stagnation in software. 

In contrast to many modern corporate R&D labs [[Bell labs asked people to do useful things but left them room to say huh that’s funny]]. Google Brain feels like it does the same thing. And perhaps that’s why it feels like a much more ‘healthy’ corporate R&D organization. In fact a lot of the pure AI work feels a little bit like this targeted dicking around. Except that they actually don’t take it the one step farther to be an experimental product.

This “targeted dicking around” could be a different way of describing what hanging out in [[The (idea) valley of death]] looks like! 🤔  [[An organization to generate quantum technology leaps and bridge the idea valley of death]]

Targeted dicking around requires [[Slack - concept]] that you don’t have at startups or in academia, and increasingly don’t have in corporate R&D either. [[R+D orgs are answerable to shareholders both in scope and timescale]].

### Related
- [[Bell Labs enabled free radicals]]



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How Tech Loses Out over at Companies, Countries and Continents

Magic Leap is a good case study of a potentially amazing technology killed by startup constraints

25 Oct 2020

General-purpose technologies need pitchfork development

The NSF could partner with philanthropy to unlock new general purpose technology

# Ideally corporate R+D enables work on a general purpose technology before it’s specialized 
# Ideally corporate R+D enables work on a general purpose technology before it’s specialized 

Specialization has a complicated relationship with new technologies. New technology will never[^1] be as good as good as old technology along every dimension. This failure of Pareto-superiority is why [[Frontier technologies need to start in niche markets where they are especially valuable]]. It’s rare that a technology can do well in a niche market without *some* specialization. If you imagine the straightest path that a technology can take to its most powerful or general use[^2], the specialization work to fit into niches can require larger or smaller diversions from this path. These diversions take the form of everything from technology development, to marketing, to building sales channels for a company. Going from niche to niche is essential, but you can also get stuck in a niche or jump onto a different development path altogether. [[Elon is the master of charting paths between niches]]. More time and resources ([[Slack - concept]]) can enable you to pick an “optimal” sequence of niches or search around for yet-unknown niches instead of being forced to hop into the nearest or most obvious ones. In other words, if [[Decoupling from market discipline is like cave diving]], corporate R&D can act like extra oxygen tanks. 

I don’t know how often I’ve seen a presentation from a grad student or professor that abstractly goes like “we’ve invented this incredible technology that could potentially do <amazing thing> however it will take a lot of work to get there, so we’re starting a company to build a product to do <kind of pathetic thing that will still require a lot of specialization and company-building> in <domain totally unrelated to <amazing thing>>.  While I’m usually sure it’s doomed to failure, it’s unfortunately the best move given history and [[§Startup Constraints]]. First, many successful startups *do* look like they started in a tiny scoffable niche  - Tesla (weird rich people), NVIDIA (gamers), PayPal (Beanie Babies on eBay?), Apple (hobbyists), Twitch (life live-streaming), Amazon (books) … the list goes on. However, each of these weird niches didn’t require huge diversions from the critical path.[^3] Second, ‘start in a niche’ is folk startup wisdom *for a reason*. History is littered with the corpses of startups that were going to be the next platform or [[General purpose technologies]] as soon as they launched. General Magic, NeXT, Quibi, Atrium, Rethink Robotics, and of course Magic Leap [[Magic Leap is a good case study of a potentially amazing technology killed by startup constraints]]. Many others that started with grand ambitions were forced to crawl into a niche to survive - Kindred Robotics comes to mind. At the same time, startup investors want to see *massive* potential returns. ‘Find a compelling story about how a niche becomes a billion dollar market’ puts a technology between a rock and a hard place.[^4] 

In most cases, it wouldn’t have been feasible to do the necessary work to find or develop for a better niche in an academic setting either. While that work still requires “research” it also requires focus and systems engineering, both things that academia does not support for a slew of reasons. [[Academia is not a good environment for systems engineering]]. [[Academia incentivizes novelty, not focus]]. 

It’s of course possible that I and others just overestimated the potential of many of these technologies. However, the examples of technologies that were massively impactful only after “hanging out” in a corporate research labs for many years would seem to argue otherwise.  The [[Transistor]], [[Public key cryptography]] and  the [[Graphical User Interface]] (and personal computing in general) come to mind. Ideally corporate research labs provide the environment for to do the work to get a technology to a point where it’s viable for a ‘useful’ niche and enable it to find that niche in the first place. 

In addition to simply having longer time scales, less existential risk, and larger budgets than most startups, there are several specific ways that corporate R&D labs (used to) help technologies find good niches that startups and academia didn’t provide.

When you’re still trying to figure a technology out, it’s not clear which skillsets you want in the room. Corporate R&D allows there to be people floating between different projects loosely creating and breaking collaborations. [[Bell Labs enabled free radicals]].  To get the same effect at a Startup, you need to either find a magical individual who has gone deep on multiple areas (M shaped individual?) or hire people who might ultimately turn out to be useful. 

[[Bell labs asked people to do useful things but left them room to say huh that’s funny]] - often that moment of “huh that’s funny” can lead to the useful niche. 

 [[Healthy R+D orgs feel like they have very smooth project rampups with high ceilings]] - the discontinuous rampup implicit in a high-growth startup can force premature committal to a specific niche and the ceiling imposed by academia can prevent you from doing the work to accurately test a niche in the first place. 

Of course, this is all talking about an idealized corporate R&D organization, which arguably has become exceedingly rare. The need to produce demos for corporate higher-ups may serve the same ‘specialization forcing function’ as startups. One way to look at this would be to ask ‘how has the *management* of corporate R&D changed over time? On the hypothesis that [[People who have done a thing should be in charge of a thing]].  On the other hand, The [[Mother of All Demos]] was in fact a demo. Same with SpaceX live fire/other Elon musk things. So the upshot might not be that “demos necessarily force specialization” but that [[Demos are like afterburners]] - applied strategically along a planned path they can allow you to jump gaps you would otherwise be unable to cross, but applied whenever you feel pressure will leave you without any fuel.

### Related
-  [[Ideally corporate R&D enables targeted dicking around]]. 

[^1]: I will say this very aggressively in the hopes that I am wrong. [[Cunningham's Law]]
[^2]: This idea might be a fallacy. Arguably there is no platonic “ultimate stage” of a technology and whatever a technology evolves into is indelibly touched by the different specialized forms it needed to pass through. 
[^3]:There are a number of just-so stories I could tell about why these university spin-offs are different than the list of successes - most of those on the list were not deeply new technology, their founders were brilliant and plotted the exact path to success, it’s easier to go into new niches with software and chips, they got lucky, I’m a moron etc. However, the empirical evidence is that so many niche-seeking startups built around new (genuinely cool) technologies fail to help that technology realize its potential. 
[^4]: I’m *not* trying to say VC and startups suck and are broken! There are many amazing things that *have* come out of the system. What I am asserting is the incorrectness of the idea that “if it wasn’t a viable startup it would never have been able to be amazing for the world in the long run”

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Understanding a thing has to do with intuiting the affordances of a thing

Many things cannot be measured well

When ‘talent’ isn’t code for ‘specialized training’ it means the role or industry has not been systematized

Paul Graham’s essays are powerful because they demystify things

Treating Science Fiction as case studies from a future history

The Categories Were Made for Man, Not Man for the Categories

In order to extend a heuretic it must be legible to you

Make precise predictions

Being mystifying is a way to hedge

Hunch, notion, idea

The two ways to enable action is through legibility and trust

A good prediction enables new thoughts and actions by being non-obvious and creating agency

§Demystification and Thought Leaders

Creating tight problem definitions is valuable

baldwinModularityDesignComplex2006

Lots of innovation is stifled because of the overhead of going off of the beaten path rather than direct forbiddance

Write down your hypotheses

Tech people are bad at politics

Precise visions are more likely to happen

Just because a system can  do a thing does not mean all instantiations of that system can do that thing

The structure of the tech tree can inform actions that are short term suboptimal but long term useful

Categories that are coupled to metrics tend to take on a life of their own

There is a tradeoff between trad creditability and the ability to do something weird

 Cellular Automata, Computation, and Physics

Daniel Correa conversation 29 Jul 2021

Legible novelty is the worst

# Legibility enables action
[[Understanding a thing has to do with intuiting the affordances of a thing]].
You know the possible moves you can make and can compare them. The mental model of a thing or process allows you to predict “if I do X, Y will happen.” 

By contrast Mystification prevents action. Mysticism forces you to consult the oracle before every action.

People are hesitant to create new organization structures not because there’s anything stopping them but because what is allowed or disallowed is not legible. [[Nobody has any idea what the affordances of human systems are]].

Legibility enables action because it removes the need for [[Trust]]. [[Trust enables action]] but [[Trust is hard to scale]].


 
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Research has many orthogonal and non orthogonal classification axes

stokesPasteurQuadrantBasic1997

Big H hard problems are those that need a discovery to solve

Edison’s Quadrant

Notes on the decline of unfettered research

Andy Matuschak conversation 8 April 2022 around funders

Glossary

# Quadrant Model of Scientific Research
![](../BearImages/30C8A24D-A4D4-4EFB-916E-E60A5179C263-19889-0004B861CEDD3625/B2A5C0D6-D3BF-41A1-86B2-D19675357F90.png)

Originally from [[stokesPasteurQuadrantBasic1997]]

I think the lower left quadrant might be “most research/papers/PhD theses.”  “I did a thing for a thing!” 

My issue with the quadrant model (and modification) is that real research is much more [[Nebulous]] , so I would actually plot things as a continuum instead of trying to bucket things

### Other Research Paradigms
- Evolutionary/Revolutionary from [[kuhnStructureScientificRevolutions1962]]
- Basic/Applied Research from [[bushScienceEndlessFrontier1945]] (although note that it’s been corrupted.)
- Invention/Discovery [[narayanamurtiCyclesInventionDiscovery2016]]
- Unfettered/Fettered research form [[odlyzkoDeclineUnfetteredResearch1995]]
- [[Phenomena-based cycles]]
- [[Heilmeier — Licklider — Braben — Elon quadrants of Research Management]]
- The clarity of critical paths and goals from [[raoGUTSGrandUnified2018]]



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alexanderStudiesSlack2020

Institutions are the second level of a group selection evolutionary system

Most institutions have become cancerous

Systems must take performance hits to get out of local optima

The value of planning is inversely proportional to the cost of experimenting

Heat cycles for democratization and cutting edge experiments innovation and discovery

The word ‘novel’ is used as an idea bludgeon in academia

Peer review has failed as an institution

Competition and lack of slack  creates specialization

Systemic decay theory of stagnation

Efficiency

Optimizing individual components of a system is often at odds with the system itself

Classical Liberalism defaults towards gridlock

Bell Labs and AT&T had timescale alignment

Culturally we expect modern organizations to become a monopoly

Some 80’s deregulation may have been a bad thing

Astro Teller conversation 1 Feb 2022

Getting to new optima is hard

Margins and innovation have a complicated relationship

Technology doesn’t solve everything but it does generate growth which arguably does solve everything

A consolidated competitive ecosystem creates a number of effects

Some ideas take a large chunk of resources to assess

How do you deal with the tradeoff that technology commoditizes things but high margins are necessary to invest in technology?

If there is a possibility for a monopoly, an institution is either nonexistent or worthless

Notes on resources around market failure

‘Have your cake and eat it too’ life-games have led to a toxic society

Notes on the changing structure of American Innovation

# Slack - concept 
# Slack - concept 
The canonical article: [[alexanderStudiesSlack2020]]
Coined by [[Zvi Moskovitz]]



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Phenomena-based cycles

arthurNatureTechnologyWhat2009

X-punk imagines a world dominated by X

Focused play enables serendipity

Computers are not great at saying ‘huh that’s funny’

Phenomena are things that happen without a human consciously making them happen

Timesharing could be extended from digital infrastructure to physical infrastructure

Introducing Speculative Technologies Outline

Telerobotic technology can unlock collaboration and serendipity

Architecture matters for creativity

Multidisciplinary teams need to leverage different paradigmatic lenses

Unexplainable phenomena are not just indistinguishable from magic, but are magic

Tool accessibility is underrated for heuretic development

Peer review is a great system for preventing waste

# The ability to say ‘huh that’s funny’ is important for discovering new phenomena
Many phenomena are not predicted by theory, and in the [[Thomas Kuhn]]sian framework, the only way we get new theory is exactly *by* observing phenomena that don’t fit theory.  Put in a [[Thomas Kuhn]]sian framework, the ability to say ‘huh that’s funny’ is ability to notice something unpredicted by existing hypotheses.

 [[Theory can suggest where to dig for new phenomena]]  - but even then it requires the ability to recognize when a theory is implying something unexpected about the world. 

Saying “huh that’s funny” (and not just brushing it off) is actually *really hard.* How many natural phenomena weren’t investigated not because we didn’t have the tools to do so, but because people just didn’t engage with the “oh that’s funny” instinct - for example the fact that two balls of unequal mass will fall at the same rate. Whoah! One theory of how our brains work is that they literally spend all their time trying to minimize the mismatch between what we expect to observe and what we actually observe. 

Repeated observations and the ability to ‘look at things from a different angle’ both help engage with saying ‘huh that’s funny.’ If you see an anomaly only once, the rational prior is that it’s a mistake in the observation rather than a new phenomenon. The importance of repeated observations is why instruments that cost a ton per observation (like the LHC) are suboptimal. ‘Looking at things from a different angle’ is a broad term that effectively means running a slightly different experiment intended to highlight the potential new phenomenon. The importance of observation tweaking is why instruments with fixed parameters like a mars probe with only a camera and a mass spectrometer are suboptimal.

 ‘huh that’s funny’ type observations can come about in two broad ways. New observational tools can get into the hands of a few people (like the Hubble telescope, or LHC) or old tools can into the hands of many people, like telescopes becoming cheap enough that amateur astronomers can proliferate. You could call these two modes “frontier-pushing” observations and “democratized” observations. Both have been historically important. 

“Frontier-pushing” observation tools are often expensive, custom made, and finicky: requiring dedicated skills to operate and interpret the results of. As a consequence, they are usually part of well funded, ‘centralized’ research efforts tied to institutions and led by incumbents (or at least people who are good at sales.) Powerful telescopes, Scanning Electron microscopes, test reactors, early computers all match this pattern. 

As better frontier-pushing tools are created, two things happen: the processes for making them become more well-known and standardized, driving down the price; and the original users get better ones, throwing away the old tools (or selling them for cheap.) “Science advances when people can buy rich people’s garbage toys” - [[Gabriel Licina]]. This price decrease and supply increase allows more people to get their hands on the observation tools. In addition to simply more eyeballs increasing the probability that someone will see something that makes them go “huh, that’s funny”, the people using more democratized tools are more likely to be outside of a traditional institutional structure, whether it’s a specific field, a university, etc. and so they will have different rules constraining their behavior ([[Institutions shape how individuals interact]]) and so might think about what they’re seeing differently and realize “huh, that’s funny” about something the original frontier-pushers overlooked.

In an ideal world, this loop of frontier->democratization will observe new phenomena that feed back and enable new generations of frontier tools. [[Heat cycles for democratization and cutting edge experiments innovation and discovery]]. 

There are several trends that worry me about a continued ability go ‘huh that’s funny.’ 

The cost of frontier-pushing tools seems to have outpaced GDP so that only governments or consortia of governments can afford things like particle accelerators or space telescopes. Government-dependent frontier-pushing tools mean that they are inherently coupled to heavy bureaucracy, are under the control of “government approved” institutions, and if politicians no longer think they’re valuable, they will not be built. The cost also means that very few of the are built, so there is massive demand relative to the supply. This demand means that there will be gatekeepers who need to sanction experiments so it’s harder to do something “outside of the paradigm” and further explorations into ‘huh that’s funny’ observations often are “out of paradigm.” Additionally the demand makes it hard to spend time ‘dicking around’ with the tools - another common pathway to discovering new phenomena.   

There’s a class of modern frontier-pushing observation tools that aren’t dropping in price and enabling democratization the way they have in the past. Even though they’ve been around for more than half a century, there are no community owned particle accelerators. The concern is a widening gap between the cutting edge and democratized modes of phenomena discovery. However, there is a lot of hope on this front. The internet enables easier time and cost fractionation for large pieces of equipment, decreasing launch costs are starting to put space telescopes in the cost range of amateurs, and you can literally buy scanning electron microscopes on eBay. 

Modern frontier-pushing tools also require large teams to operate them - particle accelerators, space telescopes, mars rovers, etc. These teams introduce coordination costs that kill the ability to go “huh, that’s funny.”  Large teams require experiment plans that are hard to deviate from on a hunch. Group decisions are less likely to lead to high-variance observations. [[Decisions made by committees lead to median results]] And, as noted before, groups of people are more easily locked into certain paradigm lenses. [[Paradigms are lenses for looking at the world]].

Perhaps most controversially, the digitization and computerization of observations has made it harder to notice things that make you go “huh, that’s funny.” Note that on whole, digitization and computerization been on net a massive boon for research!

Until you get *very small* the world is continuous, while computers are discrete. This difference has two consequences. The first is that every input needs to be run through an analog-to-digital conversion which involves ‘bucketing’ continuous signals into discrete buckets. The choice of these buckets can make the difference between an anomaly being classified as signal or noise. It’s like a different take on [[Simpsons Paradox]]. 

 Digital measurements tend to capture a limited set of information channels - either specific wavelengths of light, only the mass spectrometer data, etc. It’s like observing the world through a little peephole with headphones on. The example that comes most to mind is mars rovers. Contrast to 19th century chemists who would look at, smell, touch, *and* lick things. 
Of course, this isn’t purely because of digitizations - pushing the limits of what can be observed requires more specialized instruments. 

Computers have enabled an entirely new way of observing the world through simulations.  However, simulations are built up from how we already believe the world works.  So while simulations can recreate emergent phenomena, they are totally blind to phenomena that don’t arise from components we don’t think are important to simulate, or don’t realize that they even exist.  [[Simulations and models often fail to capture important aspects of a real system]]. 

### Related
- [[Galaxy Zoo]]
- [[Kuhnsian knowledge creation and Popperian knowledge creation assign different first steps to the same loop]]
- [[Computers are not great at saying ‘huh that’s funny’]]
- [[Heat cycles for democratization and cutting edge experiments innovation and discovery]]
-  [[Paradigms are lenses for looking at the world]]. 
- [[Phenomena-based cycles]]
- [[Cosmic Microwave Background]]



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Donald Braben Podcast 3 Nov 2020

Bell Labs hired people before they had a role or expertise

Does a PM need to be rabidly obsessed with the thing they’re PMing?

Hunting vs Farming Ideas

# When is push or pull appropriate for innovation orgs?
# When is push or pull appropriate for innovation orgs
Almost definitionally, innovation orgs depend heavily on “talent.” [[When ‘talent’ isn’t code for ‘specialized training’ it means the role or industry has not been systematized]]. However, there seem to be at least two distinct ways that different innovation orgs approach finding talent that are tightly coupled to the ideas of ‘locus of control’ and ‘idea inception.’ [[What are the different roles in an innovation org?]]

Both DARPA and Bell Labs took the “pull” approach to people. [[Bell Labs hired people before they had a role or expertise]] and would go out and just try to hire really smart people but then would give them a project to work on. DARPA is very much a “you don’t call us, we call you” system - sometimes it’s because someone is just doing good work in an area vaguely related to DARPA’s area of interest or because DARPA has a specific program for them to run. 

Venture research on the other hand took the push approach to people (ie. The person pushes themselves into the organization). They wait for people to come to them. (This is also the case for venture capital for the most part.) 

The people who are pulled or push into the org the either push or pull *ideas*. DARPA program managers both solicit ideas from potential performers (pull) but then incept ideas in them (push). Bell Labs would both let people work on what they thought was interesting (pull) and impose company priorities (push). Venture research was pure idea pull (which is coupled with person-push). ::does this make sense?::

It’s pretty clear that [[In an innovation org, the person bearing the risk needs to feel extreme ownership over an idea]] for it to succeed. On the one hand [[New ideas need to come out of a single mind]], which might suggest that the push approach would have better results. On the other hand, people grow to feel ownership over ideas that didn’t start in their own heads all the time in grad school and throughout history. Additionally, both DARPA and Bell Labs gave people space to come up with ideas once inside the organization, which is a key difference from venture research. 

There’s also a different valence between the two approaches. The push approach has the feeling of “you convince me.” Someone needs to want the thing to happen badly enough that they’re willing to work with you to explain the idea before committing to the organization.  [[Venture research built trust by iterated meetings to refine precision around the idea]]. This approach seems like it might be more tenuous in the 2020’s than the 1980’s because of how the internet has warped engagement levels. [[The internet has warped our engagement levels]]. The pull approach has the feeling of “come join us” and requires a level of sales/convincing that joining the organization is the way to turn ideas into reality. 

One wonders how much performance-affecting bias the pull system creates. By definition the pull systems will only recruit people who are inside their sphere of attention. You see DARPA primarily pulling from people they’ve worked with before and Bell Labs inordinately pulling from a few top-level universities where other lab members had gone to. At the same time, you have to consider the uncomfortable possibility that [[Bias can enable more effective action]]. In the case of finding invention and discovery folks, the more you know what you’re looking for, the less this bias matters. 

In practice, the approach will probably end up being a mix between the two, especially for a small/new organization. One could make an argument that when you are unproven you will have a hard time convincing well-known A-players to join so leaning into the “push” mechanism is important. At the same time, the initial people you work with can shape a culture and trajectory, which makes an argument for the “pull” mechanism. On the one hand, you could say “we will front load creditability via <funding, well-known-supporters, thought leadership 🤮> so that relatively unknown people will push. On the other hand, that strategy feels cringy and incorrect for an organization that wants to be a bit under the radar. The compromise might be to figure out exactly the creditability you need to get the people you want. Of course, that becomes harder the less clear you are on the people you want to get. Which is a bit of a chicken and egg problem. One solution might be to track a gut feeling on where you fall on a spectrum of “I’m finding the right people but they won’t give me the time of day” to “I don’t even know who the right people are”

Perhaps another way of looking at it is to ask “how much knowledge does management have about the area.” At some point, if you’re sober and paying attention to a specific field, it becomes increasingly unlikely that there are high-quality people who have done enough work to actually know their shit but are not on your radar. So the question of push vs. pull might depend heavily on a recruiter’s specialization. In the case of [[Venture Research]], they were looking for people far outside their realm of expertise. Bell Labs was under a much more finite umbrella, and DARPA is somewhere in between. 

There’s a tricky question about idea inception and tension between goals at different levels of the organization. [[Research requires intrinsic motivation]] but at the same time you need that motivation to be aligned with organizational priorities unless you’re all the way on the venture research end of the spectrum. It is especially hard when you’re working towards a specific vision or endpoint. Somehow,  [[JCR Licklider]] managed to pull this off. [[Alan Kay]] talks about how old school ARPA gave them complete freedom, and yet we know that Licklider managed to coordinate several independent research groups to collectively produce [[The mother of all demos]] so obviously they didn’t actually have “complete freedom.” It’s wild speculation but I suspect that Licklider managed to “chunk up” the vision into boxes. He could then find people who already had the intrinsic motivation to explore within those boxes. This seems extremely hard. <need to finish [[waldropDreamMachine2018]]>

What are other well-known examples of “pull” organizations who get people in the door because they are smart and generally competent? Many startups claim to be this way, but whether that’s actually the case 

### Related
- [[Comparing and contrasting Bell labs, DARPA, and Venture Research]]
- [[Outlier ideas tend to come from people who are outliers in other ways]]
- [[Does a PM need to be rabidly obsessed with the thing they’re PMing?]]
- Here I am being a splitter [[Lumpers and Splitters]]
- [[Who will make the best SpecTech PMs?]]
- [[Hunting vs Farming Ideas]]

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AI research is an exception to the decline of corporate R+D

Was Bell Labs an anomaly?

# Why hasn’t Bell Labs been replicated?
# Why hasn’t Bell Labs been replicated
Is this actually true - could you argue that PARC was a replication of Bell Labs?
- [[Regulation drove many of Bell Labs’ actions]]
- [[Conversation with Daniel Windham 31/10/2019]]

### Answer
My answer is that no R&D labs *working on physical technology* meet the conditions  necessary to create a high-quality corporate R&D lab. [[Healthy corporate R+D requires a trifecta of conditions]]. Note that [[AI research is an exception to the decline of corporate R+D]]. 

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We need new institutional structures to fill the role that corporate labs once occupied

# Why is there so little slack in mission-focused research?
# Why is there so little slack in mission-focused research
There are definitely more scientists so it could be that the number of researchers has gone up faster than the number of areas of exploration and you’re just seeing the effect of more researchers per area. This saturation would be exacerbated the number of areas for cutting edge patentable research has gone down. 

The other two possibilities are cultural. There may be more of a cultural equilibrium of patenting everything that seems vaguely valuable as soon as possible instead of waiting for a higher value patent or group of patents because you know that everybody else will do the same thing. This may be exacerbated by both Bayh-Dole but also the cultural expectation of how valuable science *should* be. This cultural expectation didn’t really come about until after WWII and perhaps took years to saturate the system. The other cultural  explanation for the missing slack might be conservatism around areas of exploration. If there are more incentives for groups to  do research on known good ideas then naturally there will be fewer discoveries that nobody else was working on.  

### Related
- [[neumannOneProcess2020]]
- [[The decline of science in corporate R&D]]
- [[Is Science Slowing Down? - SSC]]
- [[There is an increasingly wide gap between the number of graduate students training for PhDs and academic positions for them to fill]]
- [[Stagnation]]
- [[odlyzkoDeclineUnfetteredResearch1995]]
- [[Solutions R&D is the right term for things that are too researchy for startups and too engineering-heavy for academia]] 



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Benʼs working notes

Bell labs asked people to do useful things but left them room to say huh that’s funny

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