§Academia Constraints

Decoupling from market discipline is like cave diving

Current value capture mechanisms are crude

When should an idea that smells like research be a startup?

§Corporate R+D Constraints

Bell Labs is one of the few examples of an innovation org that was aligned with its money factory

Startups are good at point changes

Systemic decay theory of stagnation

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

There are many tight feedback loops built into the ARPA model

Things that are not paper-worthy enough for academia and not product-focused enough for a startup

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

There are many important innovations that are just bad investments

Startup Constraints - essay

The market in for-profit organizations is fairly efficient

Profit-maximizing organizational structures can hamstring technologies whose impact depends on them

It is easier to have a multipoint mutation in technology than in evolution

PARPA could walk the line between profit and non profit

Startups  need to spend effort on sales, marketing, and productization

Startups and Academia are bad at addressing structural constraints

The Architected Innov􏰂ation Institute - Engineering Scientific Revolutions

An institution riffing on the ARPA Model could enable paradigm shifts that are not happening

# §Startup Constraints
- [[Startups need to make a lot of money or have a lot of users]]

- [[Startups need to conform to investor timescales]]
- [[Venture capital doesn’t work for things that only realize their value on long timescales]]
- [[Startups need an exit strategy]]
- [[Startups need a great story]]
- [[Startups need to produce a scalable product]] 
- [[Startups need to break development into correctly sized stages]]
- [[Startups need specific growth curves]]
- [[If a project has massive possible upside and low enough risk it is venture fundable]]
- [[Scalability and venture fundability happens when you turn a process innovation into a tool innovation]]
- [[Startups are good at point changes]]

- [[Startup Constraints - essay]]

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If you need to have the possibility of near infinite returns on VC investments how is it possible to invest in higher risk things and expect a return?

# Can you get VC-level returns by funding research?
# Can you get VC-level returns by funding research
[[Isaac Barchas]] asserts that the answer is ‘no’ -
[[Laura Deming]] and [[Jason Crawford]] assert yes

First, there’s the 

My hunch is that outside of a few 

Related:
-  [[Commercializing non-health research does not produce VC level returns]]



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§Misalignment between funders and nonprofits in research

Systems research requires a lot of work that is expensive and uninteresting

Astro Teller conversation 1 Feb 2022

Some ideas take a large chunk of resources to assess

Hunting vs Farming Ideas

The efficiency imperative makes it tough for profit-seeking organizations to take on systems research

# Efficiency biases systems towards false negatives
Before you even undertake the work to create a thing, there’s some assessment of whether it’s possible and how valuable it will be.[^4] (For some extremely nebulous definition of value — I’ll talk about that later). [[Some ideas take a large chunk of resources to assess]] (**“fat” ideas**).[^3] In other cases, a spreadsheet and well-founded assumptions can make a strong case that “it will be hard, but if we pull off all these things that don’t violate physics along this critical path, it will be incredible.” (**“Lean” ideas**). 

SpaceX’s reusable rocket is a canonical lean idea: “if we can do X (which is very hard but has a clear critical path) then we will reduce/increase this key metric my an order of magnitude, which is a complete game changer.” [^1] Software’s low cost and fast iteration speeds make many bit-based ideas lean even without clear metrics or critical paths. “Basic science”[^5] is a classic example of a “fat” idea: the curiosity-driven study of tree-frog venom leads along a circuitous route to a miracle cure. However, fat ideas aren’t just curiosity-based discovery. Most “systems research”[^6] ideas — of the sort that were the precursors of a good chunk of modern technology —are also fat ideas.[^7]   

If all you care about is big returns per dollar  (in either financial terms or “impact”) there is a clear strategy: work to quickly kill ideas and bias towards a thousand false negatives over one expensive false positive. 

Imagine that lean ideas look good after 1 unit of work and will create 1000 units of value, and fat ideas only look good after 100 units of work but produce 1100 units of value. Each idea creates the same *net* value but if you care about returns on investment you would rather spend 1 unit of work every time, ignoring every single one of the fat ideas and their potential results. In order to make it worth your while, the fat ideas would need to on average create 100000 units of value (an increase proportional to the cost of evaluating them). 

Another framing is through the lens of scarce resources.  If you have 100 units of work to deploy, your choice is whether to spend that 100 units of work on 100 lean ideas or 1 fat idea. If each project has the same expected value, you would have 100x expected value by focusing 100% on lean ideas. Lean ideas are better to work on in expected value and ROI terms.

The advantage of the lean strategy has nothing to do with whether you’re trying to capture the value you create or not — as long as you prioritize efficiency, it makes sense for both investments and philanthropic spending. 

In reality, ideas don’t fall neatly into buckets that take one of two values of resources to evaluate. There’s some continuum from zero effort to [infinite effort? The value of executing on the idea itself? (You don’t know if it will be valuable and possible until you literally complete it)]. However, because we’re talking about a scalar effort to evaluate them, it’s reasonable to draw a line that is the maximum effort you’re willing to spend per idea — everything to the left is lean and everything to the right is fat. This bucketing system means that you lose out on the marginal idea immediately to the right of the line. 

 The fact that it’s hard to distinguish between many fat and lean ideas compounds the argument for a “lean assessment only” strategy.  As a result, many research organizations either implicitly or explicitly pursue the lean strategy — explicitly preferring many false negatives over an expensive false positive. Indeed, places like [[Google X]] play up the efficiency of their process. And given the assumptions and constraints they’re operating under, they’re not wrong. 

Let’s examine those assumptions:
1. Lean and fat ideas create roughly the same amount of value on average. 
2. The difference in cost between evaluating lean and fat ideas is several orders of magnitude. 
3. There are plenty of lean ideas.
4. It’s impossible to know a-priori how much effort it will take to evaluate an idea.
5. The results of lean and fat ideas are interchangeable.  
6.  Efficiency should be prioritized.

**1. Lean and fat ideas create, on average, roughly the same amount of value**  
This assumption seems pretty reasonable — I don’t know of a comprehensive study of innovations, the value they created, and whether it was easy for people to evaluate whether they were worth pursuing a priori but there are plenty of valuable examples of both types. SpaceX, Tesla, Transistors, airplanes, AI, artificial fertilizers, the structure of DNA, atomic power (after a certain point) are all lean ideas — generally they’re characterized by either a gold rush or criticisms of impossibility to pull off. Lasers, the internet, germ theory, and solar panels are all fat ideas — generally they’re characterized by people calling them niche or useless and are preceded by a lot of “piddling around.” 

While historically, lean and fat ideas do seem to create roughly the same amount of value if you force them into a framework of scalarized value, I’m going to push back against that framework in point #5. 

**2. The difference in cost between evaluating lean and fat ideas is several orders of magnitude.**
This assumption is also pretty reasonable. Lean ideas are characterized by being able to put a lot of assumptions into a spreadsheet and possibly identifying one or two key experiments to validate some assumptions. Fat ideas often involve years of piddling around (and thus years of salaries and expensive equipment) before even having a clear idea of what the valuable output even could be.   

**3. There are plenty of lean ideas.**

The number of fat ideas (even if they would only take slightly more effort to evaluate than the fat-lean cutoff) is irrelevant if all you care about is efficiency. The frequency of fat ideas is irrelevant unless the frequency of lean ideas is so low compared to the frequency of fat ideas that you hit a tipping point where pursuing a lean strategy forces you to spend more resources throwing away ideas quickly than you would spend evaluating fat ones. Thus, the lean strategy is rational if you believe there are plenty of lean ideas. 

It’s (almost? Actually?) impossible to evaluate this assumption. My personal hunch is that a component of the [[Low Hanging fruit theory of stagnation]] is that so many institutions (rationally) pursue the lean strategy that lean ideas have become depleted. You could call lean ideas “low hanging fruit” themselves, but generally the “low hanging fruit” is understood to refer to the total effort to realize the idea, not to evaluate whether it’s worthwhile. 

My other hunch is that while the distribution of evaluation costs is continuous, it is not flat. It likely has at least two peaks — one that’s lean-esque and one that’s fat-esque. If that’s the case, institutions pursuing the lean evaluation strategy can’t just incrementally increase their threshold for leanness as lean ideas are depleted. 

The first three sets of assumptions all fit within a nice numerical framework. You can play with numbers here: [False negative bias - Google Sheets](https://docs.google.com/spreadsheets/d/1j679FlpPgl4GT6Ohi9CR0yrZCLIuVrhT7rc36D_NpF0/edit?usp=sharing)

**4.  It’s impossible to know a-priori how much effort it will take to evaluate an idea.**
 The lean strategy implicitly assumes that it’s impossible to know how much effort it will take to evaluate an idea (meta evaluation!). If it were possible to know up front how much work it would take to at least know whether an idea was worth pursuing, you could know which ideas are marginal, taking two units of effort but not 100, and evaluate those ideas as well. The dream of [[§Program Design]] as a discipline is to be able to cheaply determine how much work it will be to evaluate an idea (in some senses, an ARPA-like program is an idea evaluation). 

**5. The results of lean and fat ideas are interchangeable.**  
Collapsing value into scalar quantities assumes that the outputs of pursuing different ideas are the same in kind. That is, the *types* of innovations that will come out of pursuing only lean ideas look the same as if you pursued both lean and fat ideas. Or at least the types of innovations created by lean and fat ideas are equally desirable. 

Here is where thinking in terms of monetary outcomes violently diverges from a more nebulous concept of “value.” If all you care about is cash in and cash out, the results of all ideas are interchangeable. However, I suspect that pursuing primarily lean ideas systemically biases towards certain types of innovations. As a result, whole classes of ideas are systematically *not* being explored. It will take a lot more work to enunciate what the systemic differences are between the outputs of lean and fat ideas, but my hunch is that a lot of software and point changes are lean ideas, while many [[General purpose technologies]] and multi-point changes are fat ideas.[^2] Even ignoring which specific classes of innovations we’re missing out on by pursuing primarily lean ideas, I suspect that pursuing an “unbalanced” distribution of lean/fat ideas is unhealthy for long-term innovation because ideas feed on each other — fat ideas generate lean ideas and vice versa, somewhat analogous to [[Phenomena-based cycles]]. The bias towards lean ideas may be a component of why [[Phenomena-based cycles are stuck]]. 

**6. Efficiency should be prioritized.**
The final assumption underlying lean strategies is that efficiency (value created/effort in) is the most important thing. When you have a fiduciary duty to maximize shareholder value, *this is correct*. [[There are many important innovations that are just bad investments]]. Speaking to several high-ranking people who run corporate research labs, they constantly need to justify, not the absolute cost of the work they’re doing, but the ROI they expect. 

You would expect the unbreakable coupling between profit and efficiency to suggest a clear opportunity for philanthropic money to step into the gap and enable the fat, inefficient assessments that can unlock entirely different classes of innovation. Disappointingly, I’ve found this to not be the case. Instead, the majority of philanthropic funding decisions I’ve run into are still implicitly or explicitly dominated by efficiency. Questions like “what is the most impactful way to use this dollar?” “How do we minimize risk of failure?” “How do you know it will work?” “What will the impact of this be?” Are all trying to maximize efficiency. Efficiency is not bad in a vacuum, but it is when it is killing fat ideas at a societal level (if the assumption that fat and lean ideas are interchangeable is wrong). 

Where does this all leave us? If the outputs of lean and fat ideas do indeed generate different types of innovations, a relentless prioritization of return on investment (whether in dollars or impact) has created a world of systemically skewed innovations. Many incredible discoveries and inventions have been sacrificed on the altar of efficiency. The lean-only approach is completely rational for profit-seeking businesses. However, institutions with other mandates, like philanthropy and governments, have also been captured by the same mindset. It’s a heretical notion in the current zeitgeist (and there are many ways it can go wrong), but it would be powerful for institutions that can get away with it to prioritize things besides efficiency. Perhaps [[Efficiency is overrated]].  

### Related 
- [[Efficiency is overrated]]
- [[Justification kills play]]
- [[alexanderStudiesSlack2020]]
- [[neumannOneProcess2020]]

Thanks to [[Matt Clancy]] and [[Luke Constable]] for reading drafts of this piece and amazing ideas. 

[^1]: See [[Startup by spreadsheet]]
[^2]: See [[Startups are good at point changes]], [[We don’t have good institutional ways to create multi-point changes]]
[^3]: The “fat” and “lean” framework comes from [[raoGUTSGrandUnified2018]]
[^4]: I’m implicitly talking about research ideas here, but I think this argument applies more broadly. 
[^5]: I despise this term but it is what it is
[^6]: See [[pikeSystemsSoftwareResearch2000]]
[^7]: Digging into how to tell whether an idea is fat or lean and whether there are systemic differences between them is for another time. 



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High-risk research is a malnomer

# If you need to have the possibility of near infinite returns on VC investments how is it possible to invest in higher risk things and expect a return?
# If you need to have the possibility of near infinite returns on VC investments how is it possible to invest in higher risk things and expect a return
VC portfolios are already constructed so that any company they invest in needs to have a chance of a near-infinite valuation in order to pay for all the failure. Software companies have incredible margins because they have low capital costs and often have known sales channels and little true technology risk. If there are enough software companies that have a potentially massive valuation (which seems to be a not-slowing-down trend in 2020), wouldn’t investing in non-software companies be irrational because it’s just increasing risk without increasing potential reward?

### Related
- [[Is it possible that base rate growth in the market is actually a bad thing for innovation?]]
- [[Can you get VC-level returns by funding research?]]




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Embedded growth obligations have shifted the cultural narrative to the idea that everything can and needs to be a high-return investment

# Is it possible that base rate growth in the market is actually a bad thing for innovation?
# Is it possible that base rate growth in the market is actually a bad thing for innovation
All risky investments are benchmarked against what you can get by investing in the stock market. If the stock market actually went up at a lower rate you would need to invest in riskier things to get better returns. 

On the other hand, if base rate growth didn’t exist people wouldn’t have money to invest in the first place?



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There is a significant class of innovations that would create drastically less value for the world if their value had been captured by their creators

R+D orgs lie on a spectrum between externalized and internalized execution and benefits

How does money work in PARPA?

It is hard for a private ARPA to capture value without hamstringing impact

Can the ARPA model exist outside of the government?

PARPA will eventually spin out companies

Externalized research is a buffer against B players

Executing on multiple paths towards the same goal is hard within an organization

An Institute for Creative Technology - Riffing on ARPA

Research Blockchain

# It is especially hard to capture value from externalized research
[[It is hard to capture value from research]] and it is especially hard to capture value from externalized research. 

- The people doing the research might not want to or be equipped to commercialize it and so you need to manage the transfer with an external organization
- There is little incentive for people who do not own the IP to commercialize it - researchers would just want to get their paper out of it and move on. 
- The external organization may expect to own IP or get a huge cut of the value
- When there are several pieces, any single piece may not be that valuable 
	- Imagine creating the mouse in one place, the keyboard in another, and the GUI in another
- If the external organization doesn’t own the IP, there’s a conflict of interest and they may be incentivized to hold back any insights they don’t absolutely need to 

Are there examples of organizations capturing research from external research?
- [[Genentech was started by bringing together several pieces of existing research and subcontracting to university labs]] - this may only have worked because the founders of Genentech were also the professors of the lab. 
- In a way [[Ink and Switch]] tried this, primarily hiring contractors
- [[Deep Science Ventures]]

### Ways that you can capture value from externalized research
	- Patents and licensing 
		- Need to be enforced via litigation
		- Joint ownership is messy and requires a lot of negotiation
	- Invest in an entity that is capturing value from the research
	- Cross fingers and hope the entity that captures the value donates back to you?
	- Have the researchers have a stake in the value capture entity (a la [[Genentech]] )
	- Taxes if you’re a government
	- [[Research Blockchain]] ??? 🤣

### Related
- [[It is hard to capture value from research]] 
- [[It is hard for a private ARPA to capture value without hamstringing impact]]



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Most tech transfer offices are not profitable

List of hard things

Pay-it-forward tithing is underrated

Enabling technologies must be developed while doing serious work

Bell Labs was only profitable in conjunction with AT+T

Value capture does not always need to happen through IP

Legal structures are intimately tied to the question of how money works in an organization

It is especially hard to capture value from externalized research

Creations whose impact depends on being public generate uncertain value through not-particularly modular combination with many other things and have a large combinatorial surface area

Research requires intrinsic motivation

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

PARPAs ideal legal structure comprises both a nonprofit and a for profit

ICT Distillation

IBM spent years creating copper interconnects

ICT Outline

Omniscience is not enough

# It is hard to capture value from research
Abstractly, a lot of research tends to resemble a public good. (See [[Scientific Knowledge as a Global Public Good - Contributions to Innovation and the Economy]].)  Technically, knowledge is a non-rivalrous good. Your knowledge of airplane building does not prevent me from knowing how to build an airplane. Once knowledge is no longer secret, it generally becomes non-excludable as well. These properties make the outputs of research look a lot like public goods by default. 

[[Value capture is important for incentivizing and funding research]]. The primary way to capture the value of a public good is to privatize it. [^1] However, privatizing research is tricky. [[Current value capture mechanisms are crude]] - to capture value from research, you need to either patent it *and get paid* or build a product around it. Researchers and research organizations can also indirectly capture some of the value through credit and status that can convert to consulting gigs and speaking fees. Let’s walk through the challenges with each of these mechanisms.

### Patents
 Patents only apply to research that directly goes into a product - often there is a lot of work (and failures) by *different people* that leads to the patentable research. [[We stand on the shoulders of too many giants to give them all credit]] so it’s hard for people who pave the way for research to get a kickback from patents. Large R&D labs amortize some of this work, but the modern system of startups and academia fractionalizes the work and weights the rewards towards the people at the end of the chain, for better or worse.[^2] Research often needs to be combined with *other* research to create something really valuable. Often patenting terms are so rigid that the cost of licensing multiple patents to develop a new product kills it in the cradle. [[Patents inherently prevent a piece of IP from being combined with other knowledge]]. 

 Finally, capturing value with a patent is often widely inefficient. In an ideal situation, someone building a product that incorporates the patented process comes to you, the two of you negotiate a licensing deal, and they send you a check every year. The world is not ideal. Often, you need to *find*people who are violating your patent and threaten to sue them if they don’t pay up. Standard lawyer advice when building something is to *not* look for prior art because it decreases your liability in case you happen to reinvent something. Even if someone *does* come to license your patent, the negotiation over licensing terms can be brutal - there are no standard terms and especially for a startup it can create a drag chute on a product’s profitability that makes an already hard job even harder. Once the licensing agreement is signed, you still need to make sure that the company is paying you the royalties you’re due and sue if they’re skimping you. Many inventors have spent a lot of their lives in court over patents and sometimes wind up dying in the gutter in spite of that. 

### Products
 In order to capture research value through a product, the research needs to make a single product (significantly?) better than its alternatives. If it’s modular enough that it can easily be sold and incorporated into many other products, that’s still just a product. Products rarely succeed on the quality of their new technology alone. 

Additionally, products are coupled to companies so there are many other factors that affect the value captured by the researchers besides the research itself, or even the product. Markets, sales channels, margins, fundraising, perception, etc. all make or break companies independent of their products.  [[The best technologies don’t always win]].  

This is all to say that just as it’s a long and windy road *to* a productizable piece of research, it’s also a long, windy, and narrow road to successfully productizing that research. Arguably, the work to productize the research is equally or more valuable than the research itself. 

A side note: Pharmaceuticals are unique in their productizability. It’s easy to trace new molecules back to the scientists in the lab and those molecules are patentable. Drugs demand is relatively little work to go from research to a product. You don’t need to worry about design, usability or specific use cases when taking a drug to market.  Scaling, manufacturing, and tweaking are of course hard and should not be ignored. If the drug does what it says there is close to zero market risk - people don’t like to die. The intertwined standardized FDA approval process combined with the Pharma-insurance complex means that there is almost no channel risk either. This is all to say that pharmaceuticals might not be the best exemplar for capturing value from research. 

### Indirect Value Capture
 Researchers can also capture value from their research by consulting with companies who could benefit from that research, getting speaking fees, selling books, and just generally acquiring social status. While in ways this can be good because it encourages people to spread knowledge as far and wide as possible, those same forces also incentivize exaggeration, sensationalization, and at worst, falsification (see: replication crisis.) It also pushes research to try to grab all the credit for themselves - instead of trying to create a monopoly on the research itself, researchers can capture monopoly rents on research credit. [[Value capture does not always need to happen through IP]].

### Is uncapturable value actually valuable? 

One could make the argument that if a piece of research doesn’t lead to a valuable product or patent then it isn’t valuable itself. While [[Someone needs to buy manufactured technology eventually in a monetized economy]], there are *many* pathways by which research can eventually end up in those products. Some of those pathways might enable researchers to capture value with [[Better value capture mechanisms]](science coin!) I would argue that the value of other pathways are inherently uncapturable.

There are many pieces of research that would make many products a little bit better but not enough to be worth the overhead of a patent and licensing, and they aren’t modular enough to be a product in and of themselves. Imagine a manufacturing tweak that saved thousands of companies $100 over many years. Valuable, but not enough to license on either side. This situation might be remedied by better mechanisms. 

Some impactful research resembles [[Problems where it is easy to know whether an answer is correct but hard to get to that answer]].  This situation applies to a lot of design work and best practices. Arguably you could patent these, but the work to hunt down and sue everybody who used it would require massive resources and perhaps just lead to people taking the hit and not using it in the first place. It’s questionable whether better mechanisms could help here, though you could make an argument that in the same way that the iTunes Store drastically decreased piracy, better mechanisms could make it easier to give kickbacks. 

[[We stand on the shoulders of too many giants to give them all credit]] - research often follows circuitous routes and sometimes it’s not even clear who you’re building on or you are separated though so much time that it’s impossible for them to capture some of the value they create. If you build a product with the help of a fifty year old paper, do you give some royalties to the author’s heirs? 

While it’s not strictly uncapturability, [[There is a significant class of innovations that would create drastically less value for the world if their value had been captured by their creators]]

There’s also just a lot of value that doesn’t turn into money. How would even the most sophisticated IP mechanisms have made [[Norman Borlaug]] a bajillionaire? 

While better value capture mechanisms may help, we also need better social technology ([[Pay-it-forward tithing is underrated]]) to fund and reward research that is truly a public good. 

### Related
- [[Patents have become more BS over time]]
- [[Do patents work better when firms are smaller or more uniform size?]]
- [[Market failures are actually failures of the existing institutions to allow markets to work]]
- [[Market failures are coupled to externalities]]
- [[§PARPA]]
- [[Michael nielsen re david d value of creative work twitter]]
- [[Is it possible that there are just different scales that value capture can happen on?]]
- [[You need a certain scale for technology development to be worthwhile]]

[^1]: [[Value capture is a utilitarian fantasy]], but it does encapsulate a lot of practical concepts around incentivizing and funding things that I (and hopefully many other people) want more of in the world. 
[^2]: [[Research should be treated like infrastructure]]



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arthurNatureTechnologyWhat2009

Public key cryptography

It is hard to capture value from research

Foldit

§Augmented Knowledge Generation

The creation of a heuretic has two steps - conception and implementation

It is nebulous a priori which research should produce public goods vs private goods

Purpose behind ICT Writeup

Using crowdsourced non-experts to perform optimizations

# Problems where it is easy to know whether an answer is correct but hard to get to that answer
The canonical example of this kind of problem is  public-private key cryptography where it’s very simple to see if a private key is correct because multiplying it with a public key gives an easily testable value (Need to actually understand how this works.) However figuring out the key from the value would take an obscenely long time to compute. 

Systems that obey physics generally have this property - this is why it was possible to make fold it. It’s hard to know how a protein will fold, but you can check whether it is folded correctly just by asking “does this obey physics?”

This concept partially comes from [[Reinventing Discovery]]  which says that successful collaborations tend to have a gap where it is hard to come up with a solution and easy to recognize a solution as good.

### Related
- Art
- The idea of the checksum
- [[Public key cryptography]]



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A normal for-profit structure would hamstring an ARPA-riff

# The market in for-profit organizations is fairly efficient
The barriers to creating a for-profit organization boil down to initial costs, talent, and long term funding. All of these barriers have become low enough that even crazy ideas that are good investments should tend to get funded.

The costs to starting a company are low - even if you need a lot of equipment because it is relatively easy to borrow lab space or equipment time. The startup ideology has pervaded society to such an extent that even [[People who should not be starting companies are starting companies]].

Socially, entrepreneurs are revered and people have been so indoctrinated that ‘stupid’ ideas can become billion dollar companies that there isn’t much inhibition the talent front.

On the funding side, there are more early-stage VCs than ever and despite the fact that technically [[Venture capital doesn’t work for things that only realize their value on long timescales]], the sexy success of SpaceX has encouraged at least some of them to bet on long term projects that could be wildly valuable. [[If a project has massive possible upside and low enough risk it is venture fundable]]. Additionally, angel investing has become a status symbol in some circles, pushing capital’s risk tolerance even farther. 

In combination these factors mean that the for-profit ventures that would be good investments but are not being started or funded are rare and on the margin. Of course, [[There are many important innovations that are just bad investments]].

Perhaps the place where they are inefficient is actually at the super capital-intensive end. The [[Long Term Stock Exchange (LTSE)]] will test this. 

### Counterargument
The counterargument to this assertion is that the success stories of impactful companies do seem to be incredibly contingent. Success depends on the right people being in the right place at the right time and being willing to doggedly persevere. Are there *systemic* ways to increase the rate of these contingent events?

### Related
- [[§Startup Constraints]]
- [[It is hard for a private ARPA to capture value without hamstringing impact]]
- [[There are many important innovations that are just bad investments]]



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Efficiency biases systems towards false negatives

Malcolm Handley conversation 21 Sep 2021

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

# There are many important innovations that are just bad investments
Important innovations[^1] can be bad investments in both an absolute sense because they can’t capture much of the value they create and in a relative sense compared to other possible investments. 

Many innovations are bad investments because you just can’t capture that much of their value. These come in two categories. 
1. Innovations whose value is just inherently hard to capture. Research often falls into this category ([[It is hard to capture value from research]]) especially research that is spread between multiple organizations ([[It is especially hard to capture value from externalized research]].)  Innovations that resemble [[Problems where it is easy to know whether an answer is correct but hard to get to that answer]] are especially hard to capture from - these can be design innovations, just-right-recipes, best practices, etc. 
2. Innovations that would be hamstrung by capturing their value. [[There is a significant class of innovations that would create drastically less value for the world if their value had been captured by their creators]]

There are also innovations that are bad investments relative to other options. Low liquidity, high uncertainty, and long time horizons are all undesirable characteristics of investments and also characteristics of investments in potentially-paradigm-shifting innovations. When the stock market is providing >10% year-over-year returns that are very liquid and (perceived as relatively) low risk you need to have a convincing story that you can do *much* better than that with a low-liquidity, high-uncertainty project that won’t pay out for more than a decade. Limiting ourselves just to people to technology venture investments, you’re up against software companies that have incredible margins because they have low capital costs and often have known sales channels and little true technology risk. VC portfolios are already constructed so that any company they invest in needs to have a chance of a near-infinite valuation in order to pay for all the failure. It’s hard to claim a potential payoff higher than the one they already expect, so you’re effectively asking them to accept higher risk for the same potential reward.  [[If you need to have the possibility of near infinite returns on VC investments how is it possible to invest in higher risk things and expect a return?]]Unfortunately, the attractiveness of software as an investment renders many other innovations “bad investments” by comparison.   

Often the situation is a combination of the two situations - uncertain or even good-but-not-mind-blowing captureable value combines with capital costs, margins, liquidity, or timeline to make an innovation a bad investment for rational investors. 

### Related
- [[§Startup Constraints]]
- [[Can you get VC-level returns by funding research?]]
- [[Is it possible that base rate growth in the market is actually a bad thing for innovation?]]
- [[The market in for-profit organizations is fairly efficient]]

[^1]: Obviously the definition of an “important innovation” is nebulous. 



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A new structure for scalable research

Value capture is a utilitarian fantasy

Innovation orgs need a money factory

Venture capital doesn’t work for things that only realize their value on long timescales

Regulation drove many of Bell Labs’ actions

Productive Uncertainty

DARPA would not have a positive return

Profit is important for both practical and ideological reasons

There are many questions and issues with the idea of pay-it-forward tithing

People don’t invest in technology, they invest in businesses

Inverting the normal relationship between an R+D organization and is money factory may enable new classes of activities

Key differences between FROs and different research institutional structures

The Thiel Fellowship is a good case study of creating value by not trying to capture it

There’s lots of money out there … for good investments

# There is a significant class of innovations that would create drastically less value for the world if their value had been captured by their creators
Even if [[Creations whose impact depends on being public generate uncertain value through not-particularly modular combination with many other things and have a large combinatorial surface area]] we are still left wondering “how common are these creations, actually?” People trying to capture the value from their creations have generated *massive* value in the world, so maybe anything else is a corner case.  

This argument is focused on work that you could *conceivably* privatize and use to drive a for-profit organization. There is also a whole separate class of work whose value is just hard to capture. [[It is hard to capture value from research]].

### Empirical Approach 
*Note*: There are two glaring problems with the empirical approach. First, we cannot go through *every* technology so there will be inevitable cherry-picking. Second, [[Counterfactuals]] are hard. There is no way to ‘prove’ that a technology would have had more or less impact if it were public or private. With these problems in mind, the empirical approach is probably most useful to try to *disprove* the assertion that there is a non-trivial set of heuretics whose impact depends on being public. If the disproof feels weak, that is perhaps the best empirical evidence for the claim. 

One of the strongest pieces of evidence that private innovations alone can carry the torch of progress forward is the innovation ecosystem of the late 19th and early 20th century. It was an age of massive technological change ([[Vulcanized rubber]]! [[Automobiles]]! [[Airplanes]]! [[Electricity]]! [[Telephones]]!) - almost all created by private for-profit companies. 

Arguably, many of these innovations only hit the mainstream when the component technologies became public knowledge. There was an explosion of car patents in the 1880’s and 1890’s and an explosion of car *production* in the 1900’s and 1910’s, roughly tracking a patent’s 20 year lifespan. Of course, this could be completely correlational and the time gap between invention and diffusion is just how much time was needed for learning-by-doing to happen.  Anecdotally, it’s telling that safety glass was patented in 1905 and became standard equipment in 1926.  

None of these technologies were complex enough that you couldn’t basically figure out how it works by taking it apart nor did they require up-front capital costs inaccessible to individuals without institutional backing. That means that almost by default the technologies became public knowledge as soon as it was sold. The sufficiently low cost and complexity combined with the cost of acquiring and enforcing patents in multiple countries at once meant that while private, for-profit organizations were creating the technology, it was virtually impossible for a single organization to blunt its impact across the whole world. 

Each of the ‘charismatic’ technologies we think about from the late 20th century were “final goods” with relatively small functional surface area. Additionally, these technologies could become good enough to have *some* market with relatively low-complexity component parts that could be created in-house. In situations where those component parts were artificially private thanks to patents (like the Wright brothers’ patent on coupled wing-warping/rudder control for airplanes) the invention’s impact was (arguably) heavily suppressed until it was made public. [[Arguably patents held back the airplane industry]]. 

The upshot is that almost no Industrial Age technologies meet the criteria that we would predict should lead to being hamstrung by being private.  Strictly enforced patents on the technologies that approach the criteria (like airplane control) did hamstring impact in the US where the patent was in effect. 

So which technologies would meet our criteria and were they public or private? The age of chemical engineering, especially process innovations, that began in the early 20th century seems like good hunting ground. Chemicals and the scalable processes to make them are rarely a final product and can be tuned for many different purposes. 

The [[Haber—Bosch Process]] is one of the most charismatic chemical processes. It also turns out to have been made public through a non-exclusive license at gunpoint. From [[Enriching the Earth]]:
`The first transfer of the Haber–Bosch process abroad was a result of the Versailles Treaty, which the defeated Germany had to sign in 1919. By its terms, BASF was obliged to license construction of an ammonia plant with an annual capacity of 100,000 t in France. `

It would be an entire (worthy!) research project to discern the licensing practices around other chemical processes. However, skimming through the history of the heavy hitters, there seem to be repeated references to multiple companies bringing them to market. ([[Not Counting Chemistry: How We Misread the History of 20th-Century Science and Technology]].) Additionally, a significant chunk of the work still ended up in academic papers instead of patents, whether it was being done in universities or industrial labs. (See [[The decline of science in corporate R&D]]) The number of corporate-lab published papers suggests that at least more of the steps leading up to an innovation were public than today.

Another piece of anecdotal evidence is that before  [[The relationship of government, academia, and technology fundamentally changed in 1980 with the Bayh-Dole act]], it was hard to have exclusive license rights on federally funded research. The default flipped after 1980 to a default state where research institutions by default had exclusive rights to the output of federally funded research. 

The computer age is littered with confirmational anecdotes. [[Alan Kay]] argues that the technologies created in [[Xerox PARC]] have created trillions of dollars in value. Imagine a world where Xerox sued the living daylights out of any product that used a mouse or a GUI. I suspect the mouse and GUI would have created much less value in that world. 

Counterfactually, what would have happened if AT&T were not required to license for free all of the non-telephone patents at Bell Labs? Two plausible scenarios could have happened: Either AT&T would have had a monopoly on the semiconductor market or  [[William Shockley]] would have had an exclusive license to the technology. In the former situation, it’s likely that semiconductors would have been treated the same way as most technologies tangential to a core line of business historically have been: marginalized and deprived of the chance to live up to  its promise. An eternally expensive piece of military equipment. Considering the latter scenario, consider that Shockley was a notoriously terrible manager and Shockley Semiconductor went out of business in 1968. The traitorous eight would never have left, so Shockley Semiconductor might have persisted, but would the innovations that came out of Fairchild have happened? Would [[￼Hoerni’s Planar Process]] have been created and adopted in either situation? Poor management is great at killing weird paradigm-shifting ideas. 

How much value has Linux created? If Linus Torvald were trying to capture the value it created, how would Linux have been anything other than a shitty version of windows?

### Conclusion
Many ideas have massive impact *because* people can copy them without paying their creator.  Any mechanism for capturing value has more or less built-in friction. This friction can limit the diffusion of innovations. 

The strong argument in favor of trying to capture value is that value capture is what incentivizes and funds innovations in the first place.  Value capture is not a binary “either you capture all of the value or none of it” but a question of how much of it you capture and how you capture it. Arguably Google (and many other companies) have created much more value than they have captured and may have created *less* value if its creators hadn’t tried to capture that value. [[tensions]]. However, these companies generally are not making their money off of innovations with large surface area that generate uncertain a priori value through not-particularly modular mechanisms. [^1][[Creations whose impact depends on being public generate uncertain value through not-particularly modular combination with many other things and have a large combinatorial surface area]].

 [[Current value capture mechanisms are crude]] - patents are legal monopolies and create limits by definition. [[Better value capture mechanisms]] could create a world where any innovation could create as much value as possible *and* its creators could be rewarded. 

I don’t disagree that we need better value capture mechanisms, and perhaps its a failure of imagination but I don’t know how you can’t have value capture without introducing *some* friction into the system in order to track contributions and forcibly extract money from people who are keeping more than fair share (the equivalent of suing someone who isn’t paying the licensing fees on a patent.) 

Given these considerations and the fact that this class of innovations seems to become more prevalent as the complexity of technology and its dependence on research pipelines increases, it seems clear that there is an unfortunate tradeoff between impact/value created for the world and value capture at the technological frontier. 

## Big List O’ Case Studies
### Public things where the counterfactual is probably less impact
- The semiconductor
- ARPA net
- GUI
- GPS

### Private things where the counterfactual is probably more impact
- CRISPR
- SABER engine
- APM
- GPT3

### Public things where the counterfactual is probably more impact
- Rockets (?) 
- OpenBCI

### Private things where the counterfactual is probably less impact
- Li-Ion batteries
- Google Algorithm
- Xerox copier

### Related
- [[It is especially hard to capture value from externalized research]]
- [[It is hard to capture value from research]]
- [[It is hard for a private ARPA to capture value without hamstringing impact]]
- [[Value capture does not always need to happen through IP]]
- [[We stand on the shoulders of too many giants to give them all credit]]
- - [[Venture capital doesn’t work for things that only realize their value on long timescales]]
- [[Technology increases the number of externalities in the world]]
- [[Profit-maximizing organizational structures can hamstring technologies whose impact depends on them]]
- I bet [[Anton Howes]] has opinions about this 

[^1]: Ironically, Google may be an outlier here because of billions of eyeballs + ads.



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There are many important innovations that are just bad investments

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