How can we enable more science fiction to become reality?
If you want to do something, it usually pays to study those who have done that thing successfully in the past. Asking ‘what is this outlier’s production function?’ can provide a starting point.
DARPA is an outlier organization in the world of turning science fiction into reality. Since 1958, it has been a driving force in the creation of weather satellites, GPS, personal computers, modern robotics, the Internet, autonomous cars, and voice interfaces, to name a few. However, it is primarily limited to the domain of defense technology – there are DARPA-style ideas that are out of its scope. Which emulatable attributes contributed to DARPA’s outlier results? What does a domain-independent “ARPA Model” look like? Is it possible to build other organizations that generate equally huge results in other domains by riffing on that model?
Gallons of ink have been spilled describing how DARPA works1, but in a nutshell here is how DARPA works. Around 100 program managers (PMs) with ~5 year appointments create and run programs to pursue high-level visions like “actualize the idea of man-computer symbiosis.” In these programs they fund researchers at universities and both big and small companies to do research projects of different sizes. Collectively, groups working on projects are called performers. Top-level authority lies with a Director who ultimately reports to the Secretary of Defense.
DARPA has an incredibly powerful model for innovation in defense research, and I believe an abstract ‘ARPA Model’ could yield similar results in other domains. In this piece I’ll explain in detail why DARPA works. I’ll use that description to feel out and describe to the best of my ability a platonic ARPA Model. I’ll also distill some of the model’s implications for potential riffs on the model. Incidentally, I’m working on just such an imitator, and in future essays, I’ll explain why this model could be incredibly powerful when executed in a privately-funded context.
This document acts more like a collection of atomic notes than a tight essay – a DARPA-themed tapas if you will. The order of the sections is more of a guideline than a law so feel free to skip around. Throughout you will come across internal links that look like this. These links are an attempt to illustrate the interconnectedness of the ARPA Model.
There are two stand-alone pieces to accomodate your time and interest: a , and the . The distillation is meant to capture and compress the main points of the full work. Each section of the distillation internally links to the corresponding section one level deeper so if you want more info and nuance you can get it.
I would rather this be read by a few people motivated to take action than by a broad audience who will find it merely interesting. In that vein, if you find yourself wanting to share this on Twitter or Hacker News, consider instead sharing it with one or two friends who will take action on it. Thank you for indulging me!
At the end of the day the ARPA Model depends on badass program managers. Why is this the case? PMs need to think for themselves and go up and down the ladder of abstraction in an unstructured environment. On top of that they need to be effective communicators and coordinators because so much of their jobs is building networks. There’s a pattern that the abstract qualities that make “great talent” in different high-variance industries boils down to the ability to successfully make things happen under a lot of uncertainty. Given that pattern, the people who would make good DARPA PMs would also make good hedge fund analysts, first employees at startups, etc. so digging into is important. More precise details about what makes a PM good prevent you from going after the exact same people as every other high-variance industry. When ‘talent’ isn’t code for ‘specialized training’ it means the role or industry has not been systematized. Therefore, despite all the talk here and elsewhere about ‘the ARPA Model’ we must keep in mind that we may be attributing more structure to the process than actually exists.
DARPA program managers pull control and risk away from both researchers and directors. PMs pull control away from directors by having only one official checkpoint before launching programs and pull control away from performers through their ability to move money around quickly. PMs design programs to be high-risk aggregations of lower-risk projects. Only 5–10 out of every 100 programs successfully produce transformative research, while only 10% of projects are terminated early. Shifting the risk from the performers to the program managers enables DARPA to tackle systemic problems where other models cannot.
The best program managers notice systemic biases and attack them. For example, noticing that all of the finite element modeling literature assumes a locally static situation and asking ‘what if it was dynamic?’ “The best program managers can get into the trees and still see the forest.” Obviously, this quality is rather fuzzy but leads to two precise questions:
The first question suggests that you should seek out heretics and people with expertise who are not experts. The second question suggests building structured frameworks for mapping a discipline and its assumptions.
A large part of a DARPA program manager’s job is focused network building. DARPA PMs network in the literal sense of creating networks, not just plugging into them. PMs meet disparate people working on ideas adjacent to the area in which they want to have an impact and bring them together in small workshops to dig into which possibilities are not impossible and what it would take to make them possible. The PMs host performer days — small private conferences for all the people working on different pieces of the program where performers can exchange ideas on what is working, what isn’t working, and build connections that don’t depend on the PM. 2 is a paragon here. He brought together all the crazy people interested in human-focused computing. On top of that, he also helped create the first computer science lab groups. PMs also build networks of people in different classes of organizations – government, academia, startups, and large companies. These connections smooth the path for technologies to go from the lab to the shelf.
DARPA PMs need to think for themselves, be curious, and have low ego. Why does this matter? When you are surrounded by smart, opinionated people the easy option is to either 100% accept what they’re saying because it’s eloquent and well-thought through or reject it outright because it sounds crazy or goes against your priors. Thinking for yourself allows you to avoid these traps. PMs need to be curious because building a complete picture of a discipline requires genuine curiosity to ask questions nobody else is asking. A large ego would lead to a program manager imposing their will on every piece of the program, killing curiosity and the benefits of top down problems and bottom up solutions.
DARPA is incredibly flexible with who it hires to be program managers. There are legal provisions in place that let DARPA bypass normal government hiring rules and procedures. Hiring flexibility is important because PMs are the sort of people who are in high demand, so they may be unwilling to jump through hoops. Bureaucracies ensure consistency through rules – minimal bureaucracy means there are no safeguards against hiring a terrible program manager so the principle that ‘A players hire A players and B players hire C players’ is incredibly important.
DARPA Program managers have a tenure of four to five years. This transience is important for many reasons. Transience can inculcate PMs against the temptation to play it safe or play power games because there’s only one clear objective – make the program work. You’re out regardless of success or failure. Explicitly temporary roles can incentivize people with many options to join because they can have a huge impact, and then do something else. There’s no implicit tension between the knowledge that most people will leave eventually and the uncertainty about when that will be. Regular program manager turnover means that there is also turnover in ideas.
Why do people become DARPA Program managers? From a career and money standpoint, being a program manager seems pretty rough. There are unique benefits though. It offers an outlet for people frustrated with the conservative nature of academia. The prospect of getting to control a lot of money without a ton of oversight appeals to some people. Patriotism is definitely a factor, and hard to replicate outside of a government. Being a PM can gain you the respect of a small, elite group of peers who will know what you did. Finally, there may be a particular technological vision they want to see out in the world and DARPA gives them the agency to make it happen in unique ways.
Opacity is important to DARPA’s outlier success. Congress and the DoD have little default oversight into how a PM is spending money and running a program. Opacity removes incentives to go for easy wins or to avoid being criticized by external forces. Of course, opacity can also be abused in too many ways to list, so it’s important to ask: How does DARPA incentivize people not to abuse opacity? DARPA’s small size and flat structure enable peer pressure to work in positive ways. Finite tenures either make people want to utterly crush it or not care at all. The former happens when you empower driven program managers.
The government’s influence on DARPA is buffered by opacity and the director. Opacity is especially important for DAPRA because a source of money like Congress that has many opinions exacerbates the incentive to ‘play it safe.’ Committees lead to median results and ensuring that any action you take is acceptable to a committee is almost as bad as the committee determining those actions. An opinionated director is the lynchpin keeping DARPA focused on long-term ideas that nobody is asking for (yet.) At several points in its history, the director went to bat to keep DARPA from being dissolved or absorbed into the military as a more “normal” R&D organization.
DARPA does multiple levels of top-down problem generation and bottom-up solution generation. In some ways PMs act as ‘bottom-up’ idea generation – often creating the idea for the program and soliciting project ideas from the community. In other ways PMs act as a ‘top down’ force by pushing researchers to work on a well-defined problem. DARPA completely sidesteps the always-important question “is top-down or bottom-up better?” by doing both.
The transient nature of most people at DARPA enables ideas to be revisited. Obviously institutional memory lasts longer than any individual but memory of any specific programs dies out quickly. There is only one PM running any given program and people pay much more attention to their own work than other people’s. This transient memory about specific ideas allows them to be judged on their own merits instead of dealing with baggage from the past. The ability to revisit ideas enables DARPA to explore ‘unexploited Leonardo Ideas’ – good ideas that are before their time.
DARPA is relatively tiny and flat. As of April 2020, DARPA has 124 staff and three layers of management. That number is right around Dunbar’s Number – just small enough for one person to know everyone in the organization. The small organization means that there are no “group projects” so every PM is directly responsible for the program they’re working on and you can’t have slackers. Small size also helps keep PM quality high by removing pressure to hire a lot of people.
DARPA Employees aren’t paid very much compared to what they could be. In 2017, a program managers’ estimated salary was ~$90k compared to the $170k+ an experienced technical PhD could expect even outside of software engineering. There is a positive and a negative argument for low pay. The positive argument is that it weeds out people who are just in it for the money and treat the role as ‘just a job.’ On the other hand, the low pay may weed out people who have some lower bound on what they think they’re worth.
DARPA’s aversion to people with a web presence may be how they avoid asymmetric career risk. According to a former PM, DARPA avoids hiring people with a significant web presence. In the 21st century, that’s remarkable and specific enough that it is worth digging into. People with a strong web presence tend to be focused on playing status games or at least are in a world where they realize that their career depends on public perception of their output. If you know it’s easy to shut something down it’s easier to start so less Internet presence means less grand announcements and fewer expectations. Of course, the explanation could also be that DARPA just doesn’t like people who are too loud because they like to keep things hush hush.
DARPA doesn’t do any research in house. Some subtle advantages of externalizing research:
DARPA has many tight feedback loops. Feedback loops start day one – ‘onboarding’ at DARPA is an informal process that involves mostly oral traditions and shadowing. Informal onboarding is normally a best-practice no-no but that is because most organizations don’t limit themselves to. Program managers get significant informal feedback from other PMs as they hone their program design. PMs have informal conversations with researchers, invite them to small workshops, and fund small fast projects to test assumptions. These activities set up feedback loops not just between researchers and the PM but between the researchers themselves, sometimes spawning new research communities.
The initial exploratory tranche of a DARPA program is approximately $1.5m. Most of this money goes towards small seedling projects. These seedling projects are small grants or contracts designed to help solidify that an idea is both not impossible and that it is in fact possible within scope. Intriguingly, this is in the same ballpark as a large seed round for a startup or the amount of money you need to set up an academic lab.
DARPA PMs use seedling projects to ‘acid test’ the riskiest pieces of a program idea. Seedlings are 3–9 month projects that cost $0.05M to $1M and are designed to “Move concepts from ‘disbelief’ to ‘mere doubt’” during program design. There is little oversight on the money spent on seedling projects as long as the budget is less than ~$500k. Seedlings are not about finding a solution to a problem, they’re designed to verify or disprove a hypothesis.
Every program at DARPA is intensely technically scrutinized by the tech council. The Tech Council is composed of people with technical expertise in the proposed program’s area and adjacent areas. The Tech Council Pitch Meeting is meant to be high level but council members can ask deep technical questions on anything. The tech council doesn’t have any power besides advising the director on the program’s technical soundness. A purely advisory tech council seems like a good idea because it both avoids decision by committee and keeps all responsibility squarely on the director and PM.
The ‘framework’ DARPA PMs use to create a program is by modeling the tech council. According to PMs I’ve grilled on this question, the closest thing to a framework that PMs use to guide program design is “be able to explain precisely why this idea will work to a group of really smart experts both in the area of the program and adjacent to it.” While the framework doesn’t have much structure, it does give PMs a very fixed end goal.
DARPA facilitates cross-pollination both between PMs and Performers. Everybody at DARPA has deep experience in some technical area and there is a culture of people dropping by and asking each other about the subject of their expertise. This cultural artifact is special because it would be easy for everybody to mind their own business as everybody is working on their own programs. Performers who get DARPA funding are required to share research with each other at various closed-door workshops. This sharing is valuable because they are all working on different aspects of the same problem and academia often incentivizes sharing only after work is published.
DARPA provides a derisking role for people in other organizations. DARPA derisks working on breakthrough ideas for three groups: researchers, companies, and other funders. Researchers don’t have as much uncertainty around grant proposals. PMs derisk working off the beaten path for researchers more subtly by building a community around a technological vision. DARPA derisks working off the beaten path for small companies by giving them more confidence that there will be customers for their product – either large companies or the government. For large companies, the off-the-balance sheet work to show that an idea is feasible and has evidence of demand derisks the idea to the point that they’re willing to start spending their own R&D dollars on it. Previous DARPA funding can derisk an idea to the point that more risk-averse grant-giving organizations like the NSF are willing to start funding it.
The DARPA execution framework boils down to showing that a vision is not impossible, showing that it is possible, and then making it exist. Executing on this framework is different for every program but it’s still worth going a few rungs down . At the end of the first step, a PM should have a concrete vision of where the world could go, evidence that ‘on paper’ it doesn’t violate known physics, and a precise list of experiments you would want to do before subjecting it to the scrutiny of the tech council – a group of technical experts in the program’s area and adjacent areas. At the end of the second step, a PM should have demonstration-based evidence that creating the vision is possible and a roadmap for how to get there. PMs get informal feedback throughout the program design process on whether the program is likely to be approved by the council.
DARPA is ~0.5% of the Department of Defense Budget and ~12% of that is basic research. A lot of DARPA’s budget is spent on actually assembling weapons and vehicle systems. So the math works out that only ~$400m is actually being spent on ‘basic research.’ These raw numbers raise the question – is there a ‘minimum effective budget’ to generate outlier results? If so, what is it?
DARPA is more ideas limited than money limited. This excerpt is gold: “I never really felt constrained by money,” (former DARPA director) Tether says. “I was more constrained by ideas.” In fact, aerospace engineer Verne (Larry) Lynn, DARPA’s director from 1995 to 1998, says he successfully lobbied Congress to shrink his budget after the Clinton administration had boosted it to “dangerous levels” to finance a short-lived technology reinvestment program. “When an organization becomes bigger, it becomes more bureaucratic,” Lynn told an interviewer in 2006. Why is DARPA ideas limited? Among the possibilities: A limited number of ideas fall into the sweet spot of high-risk, high reward military applications; pouring more money on ideas that aren’t ready to scale doesn’t help; and they’re not in the business of dispersion. DARPA only works on programs with a clear defense application so while their idea-limitation does not spell doom for attempts to replicate their success, it does suggest that the ARPA Model has a ceiling on its effective scale.
DARPA funds wacky things that go nowhere. DARPA programs have a 5—10% success rate and have included things like jetpacks, earthworm robots, creating fusion with sound waves, spider-man wall climbing, and bomb detecting bees. You can’t cut off just one tail of a distribution.
It is relatively easy for DARPA PMs to re-deploy funding. DARPA PMs have the ability to pull funding built into contracts with performers, which means that they can quickly move money away from an approach that isn’t working and into an approach that is working. Easily re-deployed funds lower the overhead to starting something risky and differentiate DARPA from other funding agencies, philanthropies, and venture capital.
Program Managers have the ability to deploy money without much overhead. For seedling projects, as long as it’s below roughly $500k program managers can just write a check. In the past, there was almost no oversight over PM spending after the director authorized the money. This is how J.C.R. Licklider was able to “Johnny Appleseed” computing groups all over the country in only a year. Modern program managers need to get approval from their director to write larger checks but that is still fast and low-overhead compared to other funding agencies like the NSF. The ability to deploy money without much overhead is important for many reasons including making it worthwhile to write smaller checks, opening the door to more collaborators, and just plain moving fast. Small amounts of friction can have big effects.
There are surprisingly few structural riffs on the ARPA Model. Often when people compare an organization to DARPA, they just mean that the organization hopes to enable high-risk high-reward use-inspired research. Only a few of these organizations attempt to riff on the ARPA Model’s structure. The US government has built two DARPA imitators: IARPA (the National Intelligence Agency’s ARPA) and ARPA-E (the Department of Energy’s ARPA.) IARPA might be living up to the name – funding both nobel-prize-winning quantum research and controversial forecasting research. ARPA-E has less great results. The British government has floated building an ARPA, but nothing concrete has emerged. In the private sector, Google ATAP is DARPA-esque enough to learn lessons about what not to do from and Wellcome Leap appears to be a full-on health-focused implementation of the ARPA Model.
It’s easy to set out to build a DARPA but end up building a Skunkworks. The dominant paradigm when starting a research organization is to do internalized R&D unless you’re a charitable foundation. In reality, R&D orgs lie on a spectrum between externalized and internalized, with DARPA on one end and Lockheed Skunkworks on the other. There’s nothing inherently wrong with building a Skunkworks –it just means that there are different tradeoffs and the statement “DARPA for X” is misleading.
Most DARPA clones start too big or with heavy process. DARPA started off small and informal. For years it was less than ten people. Starting big often causes heavy process –people want assurances in place to make sure their money is spent well. Starting large with large expectations and scrutiny makes it tough to execute on things that seem stupid. Regardless of size, directly copying all of DARPA’s processes leads nowhere good. Many of the processes were built up over years to fit DARPA’s exact situation.
DARPA has changed over time. Most of DARPA’s outlier output happened before APRA became DARPA in 1972 so it’s tempting to throw out anything introduced since 1972 unless it was a codification of a previously implicit rule. However, the world has changed since 19723 so it’s worth considering whether some adjustments were made to enable DARPA to more effectively operate in the world.
ARPA became DARPA in 1972 because of the increased scrutiny on military spending both in the government and outside of it. The expressly limited ARPA funding to direct military applications and gave Congress more oversight into their spending. The amendment was part of broader attitude changes towards the military both inside the government and outside of it. Inside the government there was increasing discomfort with how ARPA Program Managers could spend money on basically anything they thought was worthwhile. Unfortunately, you can’t cut off just one tail of a distribution so these constraints reduced the variance of DARPA results, both positive and negative. One might think that the technologies are so broadly applicable that smart program managers could work on anything under the umbrella of “defense” but from talking to former program managers, there are definitely DARPA-style ideas that DARPA doesn’t pursue because they are not sufficiently defense related.
Was the shift from ARPA to DARPA a focus change or a process change? The process argument is that after 1972 oversight and increased friction killed DARPA’s ability to create outlier results. The focus argument is that we just don’t see
or appreciate as many of the things that come out of DARPA because they are specifically for military use and have less broad applicability. The focus vs. process question is important because it determines whether there is anything to be
learned from how DARPA works today. The visceral excitement that comes out of (recent) former program managers talking about their time at DARPA suggests that there are many things to be learned from the current organization that is not just
Upshot: Pay attention to DARPA’s informal process and scrutinize formal process. For the most part there’s been few changes in the weird things about how DARPA’s program managers work compared to other organizations, the incentives and structure of the organization, the funding, and general shape of the process. So it is not worthless to study the modern organization. Regardless of whether or not the changes in formal process are the reason that most of DARPA’s outlier output happened before 1972, they certainly didn’t help. Therefore, if you want to replicate DARPA’s outlier success, it makes sense to pay attention to DARPA’s informal process and for the most part ignore formal process. Formal process is put into place to increase oversight and decrease reliance on trust. Formal process lets people outside the organization trust in the process instead of the people. Ignoring the formal process makes the success of an organization depend more on trust in people. This trust-dependence means that it is essential for an organization that seeks to replicate DARPA’s success to start with trust from funders and collaborators outside the organization. The trust-dependence creates a chicken-and-egg situation –by definition new models and organizations do not have a track record and the people who are most likely to create a new game are ones who haven’t won at other games.
This document is not meant to be a primer on how the ARPA Model works or a history of DARPA, although it draws on both. People have written thousands of words on both4. This document is not meant to be an unbiased presentation of facts or argue for a general thesis about the world or institutions (though it hints at some.) The goal of this analysis is to acknowledge that DARPA is a massive outlier, figure out which emulatable attributes contributed to its outlier results, and synthesize them with the explicit intention of creating more organizations that can enable more outlier results. More than anything else, this analysis is meant to guide my own action, not to be tossed into the sea of the Internet for some unknown policy maker to act on (though that would be nifty.)
The nature of outliers means that you can’t do a data-based analysis. Perhaps controversially, I think it’s foolish to try to find patterns among outliers because outliers are outliers in different ways except in the most broad strokes. Instead, I dig into the characteristics that seem distinctive and ask why they might lead to outlier results. At the end of the day, this is storytelling. But stories are powerful. Of course, it’s easy to take this approach too far and create a story about how anything weird about an outlier contributed to their success: “Steve Jobs only wore one outfit which is important because it allowed him to have EXTREME FOCUS.” I try to avoid the lure of story first by focusing on why the pieces lead to outlier performance in combination. Many people who try to replicate outliers fail by picking and choosing the pieces they want to replicate. Second, the goal here is to figure out how to make something that works, not create a cute theory. I hope that the desire to enable action incentivized me to be intellectually honest.
Is it foolish to try to replicate outliers? Every outlier is an outlier in a different way, so on its surface it seems like the answer is yes. Concretely, many people have set out to build the next Apple by emphasizing design and perfectionism and fallen flat on their face. People have even tried to replicate DARPA. , , and others are explicitly modeled on DARPA.
There are three mistakes you could make when trying to replicate outliers:
Instead of trying to copy an outlier exactly or only in broad strokes, the goal should be to deeply understand how it works and then riff on that understanding for your own situation. If it helps, imagine a Jenga tower made up of attributes of the outlier. While not all the attributes are important, many are, in an interconnected way. We need to poke each block and see which ones are structural. While few people have become outliers by copying other outliers, plenty of outliers have become outliers by apprenticing to other outliers (Ben Graham and Warren Buffet, Edison and Ford, etc.) You could think of an outlier analysis of an organization as a type of organizational apprenticeship.
The evidence also suggests that while it’s hard, replicating outlier success is not impossible. IARPA arguably has been reasonably successful –David Wineland’s Nobel prize winning quantum computing work was sponsored by IARPA and I suspect that IARPA is positioned to be to quantum computing what ARPA was to personal computing. Since, the IARPA proof point that riffing on the ARPA Model is not impossible is a good first step.
I lean heavily on internal linking within this writeup. Partially the links are an attempt to illustrate how interconnected the different components are in order to avoid the cherry-picking failure case. To avoid cargo-culting abstraction I try to explain why each component matters, erring on the side of speculation rather than on the side of “just because.” These deep interlinked explanations will hopefully enable myself and others to see where components could be changed to adjust for different applications without copying the whole thing whole cloth and expecting it to work.
If you trust me to do the analysis and want to skip straight to the conclusions. I heavily linked them as well, so you can just dig into the ones that make you go 🤔
I play fast and loose with the term “risk” – it’s mostly as a shorthand for “chance of not achieving goals.”
Economist Tyler Cowen has a habit of asking guests on his podcast about their “production function” –how do they do the amazing things they do? This is an attempt to distill the DARPA production function.
Every single description of the ARPA Model agrees that it’s all about the program managers.
When talking to people about how DARPA works you repeatedly hear “DARPA depends on amazing program managers.” Assuming this isn’t just (and I suspect it’s not) why is this the case?
PMs don’t get much structure when they’re designing and executing programs. The closest thing to a ‘program design framework’ I could tease out of former DARPA PMs is that they r. As we already noted, which involves a very strong ability to think for yourself and go up and down the ladder of abstraction in an unstructured environment. To throw some more suitcase-handle words into the mix PMs need to be good communicators and coordinators
There’s a pattern that the abstract qualities that make “great talent” in different high-variance industries boils down to the ability to successfully make things happen under a lot of uncertainty. DARPA PMs strongly pattern match against that description. Two conclusions from that observation:
PMs pull control away from directors by having only one official checkpoint before launching programs and pull control away from performers through their ability to move money around quickly. Control over direction and goals lies on a spectrum between performers —the people actually executing on the research and building with their own two hands – and directors –the people who run the innovation organization, be it a VC firm or DARPA.
On the performer control end of the spectrum are organizations like that in essence say “ok performers – here’s a bunch of money – go for it!”
On the other end of the spectrum, director control looks like NASA’s manned space program where the President has direct input into its direction. (Which is why NASA comes up with a 10 year plan every 8 years.)
Both ends of the control spectrum can lead to great results in the right situation. Performer control is effective for true exploratory research where you can’t do better than someone with good intuition playing around. Director control is effective in scenarios like the Apollo Program or Manhattan Project, where you need a massive amount of resources and alignment from wildly different organizations like Congress, academia, the military, and companies.
In a way DARPA PMs add a second axis to the control spectrum, pulling control away from both the performers and the directors. PMs pull control away from directors by having only and pull control away from performers through . It is relatively easy for DARPA PMs to re-deploy funding while it’s hard for someone to pull funding from the program manager. The ARPA Model doesn’t fall neatly into a bucket of “top-down” or “bottom-up” but instead the PMs enable DARPA to do .
In addition to concentrating control, program managers also concentrate risk. The program manager ideally creates a program where the risk lies in the synthesis of relatively low risk projects. This approach is different from either a normal funding agency or VC portfolio approach where the performers bear the most risk and those risks are aggregated into a portfolio. , so going into the main program, they should be pretty confident that what they’re paying performers to do is possible. Science policy researcher 5 that the organization accepts the risk and the PM takes it on when the director approves a program on the advice of the tech council, not when the program manager gives out a grant.
How well does assuming risk at the level of the program instead of the performer work? asserts that only 10% of individual ARPA-E projects are terminated early. That number seems quite low compared to the technically aggressive nature of the programs and while there are no official numbers on program failure rates, it’s undoubtedly much higher than 10%. There are no great ways to compare to grants, but an NSF program designed to support ‘high risk’ research had a ~10% success rate (where success was defined as producing transformative research.) High project success rates and low program success rates suggests that Program Managers are able to shift risk to the program level. Why does this matter? Shifting the risk from the performers to the program enables DARPA to tackle systemic problems where other models cannot.
“The best program managers can get into the trees and still see the forest.”
According to former PMs, DARPA’s outlier success depends on program managers who have the ability to look at an entire literature of a discipline and notice systemic biases. This essential but vague attribute of program managers is one of the reasons that at the end of the day, .
Luckily this admonition lets us dig into two more precise questions
Finding the sort of person who can find systemic biases in a discipline:
All of these attributes mean that PMs will be people who maybe look a bit ‘off’ on paper and emphasizes why it is important that .
Possible systems for finding systemic biases in an area:
It might be possible for an organization hoping to riff on ARPA to build tools that make doing these things easier. This idea is not unprecedented – DARPA itself has a program to enhance program design (metaprogram?) that resulted in . It’s directionally correct but leaves a lot of room for improvement.
out that DARPA program managers act as ‘brokers’ and ‘boundary spanners’ –terms of art for people who connect relatively unconnected clusters of people. DARPA PMs network in the literal sense of creating networks, not just plugging into them.
The idea of focused networking is important. DARPA program managers have a clear purpose for building the network –first to generate a clear target in an area, then to solicit paths towards the target, and then to make sure that the people who are executing on those paths know about each other so small adjustments to the plan can happen as frictionlessly as possible. It is easy to network in an indeterminate way, hoping that the connections you make will be useful one day. Many people go about networking in this way.
“Networking” is just jargon for ‘building relationships with people who aren’t shoved in front of you by life’ and PMs need to do this at What does this tactically look like in practice?
In the first step – showing that a thing is not impossible, PMs need to find and become friends with (ideally) everybody who is working on ideas adjacent to the area where they want to have an impact to get a sense of what’s possible. Realistically, PMs are able to get this access because they bring the possibility of funding. PMs also bring these people together in small groups to dig into which possibilities are not impossible and what it would take to make them possible. If the PM is doing their job well the people at the workshops won’t already know each other and will continue to poke at ideas together on their own. The second step of the process –showing that a thing is in fact possible – leverages the network built during the first step to quickly do .
During the third step of the process, PMs depend heavily on the network to send unique solutions their way. The PMs host performer days –small private conference for all the people working on different pieces of the program. These conferences force people to talk about the work they’re doing while they’re doing it, which while uncomfortable, enables people to share solutions to tricky problems and form more connections. You could imagine this leading to problematic correlation between results because everybody would want to copy whatever the shiniest group is doing but at this point all the performers are locked in to whatever approach they’re trying.
You could think of DARPA PMs as playing the role of a manual system. In this role, they both connect the right people at the right time and give them an incentive to help each other out.
In , M. Mitchell Waldrop talks about how 6 was always flying around to different university groups. In addition to bringing together all the people who thought they were crazy to be interested in human-focused computing, he also helped create several new lab groups. Today, a new professor needs about $1.5m to get going. Interestingly, I haven’t seen any organizations devoted to seeding labs in a structured way beyond funding new professors who would have worked on those ideas anyway.
PMs also build networks of people in different classes of organizations –government, academia, startups, and large companies. Connections between different verticals is one way that t –in the 1960's, large companies had much more academic R&D arms and startups were barely a thing. By bringing academics, startups and big companies together, modern DARPA PMs are agents of ’s admonition to “Manage the Transfer not the Technology.” That is, it’s more important to manage the transfer of the technology between different groups and organizations, than it is to make sure that it is created in the first place. This shift in the PM role is important. Two reasons standing in the way of sci-fi tinged technology that I’ve seen over and over are first: technology that needs actual manufacturing or high capital investment isn’t able to jump the gap from a lab to a startup prototype or from a startup prototype to a real scalably manufactured product and second: many pieces of technology that are amazing but don’t warrant an entire VC backed startup on their own. It seems like building connections between different organization classes while the technology is being built could address both problems.
In a way, the program manager acts like a product manager in a tech company, talking to the customer and modeling their needs. For DARPA the military is the customer but the difference is that the ‘product’ isn’t something that can be purchased (TRL 9) but something that is proved out enough that other branches of the military will scale it up.
Yes, on its surface this sounds like a platitude, but because so much of the ARPA Model revolves around program managers, it’s worthwhile to dig into why the personality traits actually matter.
PMs need to think for themselves because at the end of the day, everybody they talk to has only a piece of the puzzle so the PM needs to both put the pieces together and precisely argue for the feasibility of the final picture. When you are surrounded by smart, opinionated people the easy option is to either 100% accept what they’re saying because it’s eloquent and well-thought through or reject it outright because it sounds crazy or goes against your priors. Thinking for yourself allows you to avoid these traps.
PMs need to be curious because building a complete picture of a discipline requires genuine curiosity to Additionally, the ‘serendipity hatch’ during program execution where there is always an open call for ideas means that a program manager needs to be open to random outside solutions. Many people falsely claim they are curious, but from my direct experience DARPA PMs will have an earnest discussion with people who approach them about the craziest ideas.
Scientists working on DARPA programs usually describe PMs as funding ‘their idea’ in a proud way. At the same time, people looking at a DARPA program from the outside describe the program as clearly the PMs idea. A high ego would lead to a program manager imposing their will on every piece of the program, killing curiosity and the benefits of .
Unlike most government roles, there are no hard requirements on the sort of people who can be hired to be program managers, to the extent that there are legal provisions in place that let DARPA bypass normal government hiring rules and procedures. This is important because , so you need the ability to get people right when they’re available or work around their constraints. Additionally, the PM’s ability to is an attribute that is likely to make them clash with established structures and thus not be as heavily credentialed.
Hiring flexibility is also important because the bar for program managers is very high and so it’s just straight up hard to find people who would both be good at and willing to do the job. The only flexibility you have in that situation is on credentials and profile.
Bureaucracies ensure consistency through rules, so there are no safeguards against hiring a terrible program manager. The fact that there are no guard rails makes DARPA extremely dependent on the principle that ‘A players hire A players and B players hire C players.’ It’s a double edged sword. One reason hiring rules exist is to fight people’s tendency to hire people like themselves. That tendency leads to organizational inbreeding which DARPA has been subject to in the past.
Explicitly temporary tours of duty may also be one way that DARPA is able to get amazing PMs where they wouldn’t have been able to otherwise. If you have many options in life, it’s more palatable to go into a position that is explicitly designed around the expectation that you can have maximum impact in a few years and then go do something else.
The transient nature of program managers also makes them more immune to most of the effects of asymmetric career risk because there’s only one clear objective – make the program work. They are still subject to the bias of giving grants disproportionately to people they trust. The familiarity bias is what pushes granting committees to give grants to well-established, known researchers. However, my hunch is that biases towards trust and exposure are more solvable problems than worrying about their ability to show that their money was ‘well spent’.
Abstractly, the explicitly temporary nature of program managers allows DARPA to maintain alignment with program managers because alignment between people playing different games can happen on finite time scales but rarely on infinite ones. Unlike many organizations there’s no implicit tension between the knowledge that most people will leave eventually and the uncertainty about when that will be.
People and organizations are all playing some game that has different ways of gaining status and power. Maybe there’s something about PM’s transient nature that doesn’t allow them to play long-term games or figure out how to game them. There’s something to the fact that the program managers are not just transient, but they are transiently changing games. An academic who becomes a program manager isn’t going to worry about publishing papers. A military officer who becomes a program manager isn’t going to worry about impressing their direct superiors. .
The transient nature of program managers was only codified in the ’90s because program managers were sticking around for much longer than five years. This codification suggests that the transient nature of program managers is more than just a historical artifact.
Speculatively, there’s something about a culture that knows people have an explicitly short tenure that might actually maintain quality. You see this in lab groups, (possibly military units?), and fraternities that maintain the same culture for decades. Intergenerational culture is like a standing wave.
From a career and money standpoint, being a program manager seems pretty rough. There’s no promotion, no career stability, , you need to move to Washington DC, and you often don’t get to show off what you did after you’re out.
Like almost all government agencies, DARPA answers to the executive branch and receives funding from Congress.
There are many parts of the US government that are heavily influenced by term-level timescales. For example NASA comes up with a 10 year plan every 8 years for some weird reason. Several DARPA programs operated from at least 2012 or 2013 to 2020, which means that they successfully crossed administrative boundaries. However, term-scale incentives may have begun to break down – starting in 2001, DARPA directors began to sync up with presidential administrations.
Because , the Department of Defense itself doesn’t have direct control over which programs DARPA is running. However, the Department of Defense does put pressure on the DARPA director to work on areas that are currently relevant to the military, like counter-terrorism and insurgent warfare in the 2000s or jungle warfare in the early 1970s.
An opinionated director is the lynchpin keeping DARPA focused on long-term things that nobody is asking for (yet.) At several points in its history, the director went to bat to keep DARPA from being dissolved or absorbed into the military as a more “normal” R&D organization. This secret meta-dependence on the director makes the increasing politicization of the director potentially detrimental to DARPA and there is evidence that DARPA has shifted away from long-term disruptive work in conjunction with the probable director politicization.
Originally Congress funded ARPA through a lump sum but over time has shifted to requiring a budget for each program, including what they plan to accomplish for the year7. You know this is bullshit because the plans have statements like “Advance development of design tools for the optimization of collaborative problem solving performance in human-machine systems and systems-of-systems.” In 2003, Congress investigated and effectively defunded the Total Information Awareness Program –an expensive surveillance program riding on the heels of September 11th.
Abstractly, opacity seems important because if your source of money is constantly looking over your shoulder and judging what you’re doing, you’re going to take actions that look good. A source of money like Congress that has many opinions exacerbates the incentive to ‘play it safe’ because making sure any action you take is acceptable to a committee is almost as bad as the committee determining those actions. Decisions made by committees lead to median results. Coincident with Congress digging more into program specifics, more and more DARPA programs are becoming classified. It is complete speculation but it hints at a tension between DARPA’s desire to and Congress’ desire to have oversight thanks to a trust breakdown possibly tied to increasing politicization.
Over time, DARPA has become less opaque and the director has become more coupled to the current administration. If you buy the argument that it’s important to it leads to the conclusion that and DARPAs director is important.
Opacity removes incentives to go for easy wins or to avoid being criticized by external forces. Reporting requirements also add friction around everything from hiring to changing direction to trying crazy things to moving quickly and more.
Of course, opacity can also be abused: getting nothing done, dumping money into stupid projects or unnecessary expenses, giving contracts to performers with whom you have a special relationship, or just straight up stealing. Opacity can be abused in too many ways to list and prevent, which means that a better strategy is to incentivize people not to abuse it.
How does DARPA incentivize people not to abuse the opacity?
so it’s actually possible for everybody to know everybody. This means that everybody knows what everybody else is up to and the mechanism of peer pressure can come into play to make sure that opacity is not abused.
, so they’re out regardless of their performance. In my experience finite tenures either make people want to utterly crush it or not care at all. One way to push for the desire to crush it is simply finding self-motivated people with a lot of integrity who really care about what they’re doing. Of course, this strategy piles even more weight onto . Another way to motivate people to make the best of a temporary assignment is to enable them to be as effective as possible. The criticality of effective PMs emphasizes how important it is to minimize even small frictions – process can kill effectiveness through a thousand cuts. This observation suggests that overregulation could actually lead to a negative feedback loop of PMs feeling less effective which pushes them to the other end of the behavior spectrum for temporary positions which increases the need for overregulation. Obviously that’s an extreme scenario, but it emphasizes the need for opacity. In a way it’s like a prisoner’s dilemma.
Nominally venture capitalists are incentivized not to abuse their opacity because of carry. Program managers don’t have that incentive.
So put yourself in the situation of a Program Manager: you can’t get promoted, you’re out in five years, nobody will know what you’ve done whether you succeed or fail, and you’re surrounded by people who are complete ballers working on amazing things. You can either sit on your butt and do literally nothing, or go all out and try to make something amazing. There doesn’t seem to be any incentive to either hedge bets or make it look like you’re working when you’re not.
The big question then becomes: Bluntly, the incentives to do amazing deeds once you’re part of the organization do not make a compelling sales pitch to join.
DARPA completely sidesteps the always-important question “is top-down or bottom up better?” by doing both.
In some ways, the program manager is the ‘bottom up’ component. DARPA does an initial pass of top-down when it hires someone. The director or departing PM is 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 and they want to have them on staff. The Program manager then proposes a more explicit solution to the high level problem area and gets it signed off by the director.
In other ways the program manager is the ‘top down’ component of top down problems and bottom up solutions. When they are doing initial program design (ie. steps one and two of ) they talk to many researchers about possible solutions and solicit project ideas. During the actual execution phase, while they 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.
DARPA Program managers have a tenure of four to five years. Similarly, before 2001, directors did not stick around much longer. Obviously institutional memory lasts longer than any individual but memory of any specific programs dies out quickly because DARPA is relatively tiny and flat so there is only one PM running any program and people pay much more attention to their own work than other people’s. This transient memory about failed programs means less friction around creating a program that ‘has been tried before’ and makes it more likely that DARPA can explore ‘unexploited Leonardo Ideas’ or ‘gems in plain sight’ –ideas that are good but before their time.
how there have been multiple instances of program managers starting successful programs that they discovered later were almost the same as failed programs from the past. If there were enough people around who had seen the failure, the program manager would have had to not just argue for the validity of their program on its own grounds, but address the shadow cast by the failed program. Of course it’s rational to try something that failed in the past as long as you explicitly call out why you will succeed when they failed but small amounts of friction can have large effects. Essentially, the transient memory about specific ideas allows them to be judged on their own merits instead of dealing with baggage from the past.
It’s entirely possible that short institutional memory about specific programs could lead to people trying terrible ideas over and over again. You see that with certain forms of government, for example. If there are high epistemological standards (enforced by the tech council, informal feedback from other PMs, and the ability to do seedling projects) and there are no externalities to the failure, trying things over and over again has capped downsides. Additionally, the institutional memory is short, but not that short – you will only get a complete turnover once every ~five years, which is enough time for the constraints in the world to change.
In a way, short institutional memory about programs is like the temporal version of how federated systems like Renaissance Europe prevent disruptive changes from being completely damped out as opposed to centralized systems like Imperial China.8
As of April 2020, there are 124 staff and three layers. That number is right around Dunbar’s Number –just small enough for one person to know everyone in the organization. It’s not explicitly designed that way but I suspect that it emerged as the right number for the Director to be able to vaguely pay attention to everything that is going on and for everybody in the organization to have vague context on what everybody else is working on. There are three layers – the Director, office directors, and program managers (with a few deputy directors thrown in.) Culturally and physically DARPA is set up so everybody can talk and seek advice, so there is lots of ability for idea cross-pollination.
DARPA’s size may help minimize internal politics. The returns to politics is higher at large organizations because there is less direct accountability and any one person doesn’t have a lot of agency to change outcomes. Low potential impact makes it more worthwhile to get people to like you than produce results. On the flipside, in DARPA any program and therefore any program manager can potentially create an industry. The small organization means that there are no “group projects” so every PM is directly responsible for the program they’re working on and you can’t have slackers.
I suspect the small size also helps keep PM quality high. Quality tends to slip when there is both flexibility in who you can hire and there is pressure to hire a lot of people. Since , it becomes important to not have pressure to hire more.
The downside of the tiny flat organization is that there don’t seem to be any checks on the Director’s power, so if they don’t like a program or a person they’re out. This is why politicization is dangerous. Politicization would lead to the director prioritizing aligning their goals with factors outside of the organization and PMs aligning with the director more than with the organization’s nominal goal.
In 2017, a DARPA director is estimated at $76—130k per year and program managers are estimated at $90k. While DARPA does have leeway over salaries compared to the rest of the government, they still can’t offer the same compensation as large tech companies.
The people with the right qualifications could be making much more. Experienced technical PhDs even outside of software engineering can reasonably expect $170k+. Unfortunately, the things that make “great talent” in high variance industries just boils down to the ability to successfully make things happen under a lot of uncertainty.
It raises the question –was this more comparable to industry averages in the ’60s? From the Bulletin of the United States Bureau of Labor Statistics in 1960 a PhD Mathematician in industry could make ~$11,000 and $8,955 in government. That’s $96,000 and $78,000 today. So yes, the gap would appear to be much smaller.
There is a positive and a negative argument for low pay. The positive argument is that it weeds out people who are just in it for the money and treat the role as ‘just a job.’ On the other hand the negative argument is that the low pay weeds out people who have some lower bound on what they think they’re worth. I can only assume that the widening gap since the ’60s has exacerbated this latter point.
The low pay makes the question “” even more important.
If you try to find current and even former DARPA PMs or directors on the Internet you’ll have a hard time. DARPA avoids hiring people with a significant web presence. In the 21st century, that’s remarkable and specific enough that it is worth digging into.
Asymmetric career risk happens when you know that the downsides of doing the ’safe’ thing are capped while the downsides of doing the ‘risky’ things are uncapped. Therefore it makes sense that you would be more willing to make risky moves in an institutional context if you know you aren’t going to be judged on your actions either way after you leave.
People with a web presence tend to be focused on playing status games or at least are in a world where they realize that their career depends on public perception of their output. Internet people are often playing a game to maximize engagement. So being an Internet person could be taken as being a signal that a potential PM would have in the back of their mind “what will other people think about this?”
People are more likely to judge a crazy act positively if they know the reasons why it happened. So if the people you care about are a rather than the whole Internet it increases incentives to just go for it.
Additionally, less Internet presence means less grand announcements and fewer expectations. If you know it’s easy to shut something down it’s easier to start. Contrast this to something like Peter Diamandis and the X-Prize where there is a huge announcement and massive expectations which can quickly lead to institutional distrust when expectations aren’t met. My impression is that most people don’t take the X-Prize seriously anymore because the ratio of smoke to fire keeps increasing.
Of course, it could be more simple and DARPA just doesn’t like people who are too loud because they like to keep things hush hush.. But then maybe there is something to keeping things hush hush. If you keep things hush hush, you don’t have to deal with lock-in from publicly announcing you’re going to do something.
There is a ton of literature on how DARPA externalizes research, so I want to dig into some subtle advantages of externalizing research:
Of course there are also disadvantages:
It’s easy to conflate ARPA with Bell Labs, Lockheed Skunkworks, or Xerox PARC but they’re fundamentally different because R&D orgs lie on a spectrum between externalized and internalized and DARPA is all the way on the externalized end, while those other orgs are much closer to the internalized end. A common trap for people claiming to replicate DARPA is internalizing the majority of their work.
From day one there is a feedback loop between a new program manager and the other program managers. ‘Onboarding’ at DARPA is an informal process that involves mostly oral traditions and shadowing. Informal onboarding is normally a no-no when it comes to best practices but most organizations don’t limit themselves to. Program managers get significant informal feedback from other PMs as they hone their program design. This feedback includes whether something is and whether the design is precise enough. High quality informal feedback depends on other PMs actually caring, so this is another reason DARPA PMs need to think for themselves, be curious, and have low ego.
There are multiple levels of feedback loop between the PM and the research community during program design. The tightest loop is informal conversations with individual researchers and groups about where they see blockers and possibilities in the area that the PM can then incorporate into their program design. The PM then uses workshops to set up feedback loops between those possibilities – an idea might be good but an enthusiastic proponent could gloss over a major hole that needs to be filled. Finally, small projects test the riskiest parts of those possibilities against the world before the PM incorporates them into the program design. The workshops also set up feedback loops between previously unconnected groups of researchers focused on the program area that hopefully create new ideas and (ideally) new research communities.
PMs also set up feedback loops between different parts of an industry –academia, startups, and big companies. Setting up these feedback loops with researchers across a discipline is why
Feedback loops enable a PM to adjust, kill, or start projects as necessary during the execution of the program. Frequent contact with performers working on a project enables both the performer and the PM to incorporate new information into decisions on whether they should make small adjustments to the project’s goals and how that propagates into the rest of the program. PMs also use this information to decide whether t. Failed projects are also part of a feedback loop: “The failure (of a performer) triggers a discussion in which the first question is whether the goals were correctly specified and how they might be redefined in the light of the research that has already taken place.”
The ARPA Model also uses long-term feedback loops to maintain high quality PMs and research collaborations. A players hire A players and B players hire C players so high quality program managers make other high quality program managers want to join. Low friction interactions with DARPA and funding that enables performers to do things they wouldn’t be able to do otherwise keeps ideas coming from the community.
Even PM hiring is part of a feedback loop between the organization and the outside world. PMs are hired to explore a specific area that DARPA wants to explore. Even though it works on technology that nobody knows they need yet, DARPA needs to be responsive to changes in the world – whether it’s new possibilities (technology push) or new needs (technology pull.) This buffering between the outside world and hiring is one of the ways DARPAs director is important.
A lot of DARPA’s budget is spent on actually assembling weapons and vehicle systems. So the math works out that only ~$400m is actually being spent on ‘basic research.’
These raw numbers raise two questions:
“I never really felt constrained by money,” (former DARPA director) Tether says. “I was more constrained by ideas.” In fact, aerospace engineer Verne (Larry) Lynn, DARPA’s director from 1995 to 1998, says he successfully lobbied Congress to shrink his budget after the Clinton administration had boosted it to “dangerous levels” to finance a short-lived technology reinvestment program. “When an organization becomes bigger, it becomes more bureaucratic,” Lynn told an interviewer in 2006.
(Let’s just take a moment to stand in awe of this 😮)
Both the explicit desire to avoid bureaucracy and the low marginal benefit of money and people is another reason why is important.
Why is DARPA more ideas limited than money limited?
VC firms experience a similar effect –they tend to have lower percent returns as funds get bigger even though they *are* in the business of scaling things.
Presumably DARPA also has a lower bound on effective funding. What might that be?
Many DARPA programs that don’t go anywhere and sometimes sound stupid in retrospect. This list is meant to show how wacky some of the programs sound, especially in “Explain it like I’m Five English.” Because you can’t cut off just one tail of a distribution, funding these wacky things is essential to getting outlier results.
For , as long as it’s below roughly $500k program managers can just write a check.
Modern program managers need to get approval from their director to write larger grants and they need to work through official government vehicles like open grant calls and government websites. 😭 However, the PM is the only person reading the grant proposals and they don’t need to check with anybody before deploying the money once it’s been allocated. This process is still fast compared to other funding agencies like the NSF where there is literally a committee that deliberates over grant applications. Even large companies or universities require you to submit a request before spending a large chunk of money.
In the past there was almost no oversight over PM spending after the director authorized the money. This is how J.C.R. Licklider was able to “Johnny Appleseed” computing groups all over the country in only a year. The transition from ARPA to DARPA was coupled to more oversight on military spending, which inevitably introduced more overhead.
The ability to deploy money without much overhead is important for many reasons including making it worthwhile to write smaller checks, opening the door to more collaborators, and just plain moving fast. If it is an equal amount of pain for the PM to write a check regardless of size and the same amount of pain for a performer to apply for any amount of money, there will be some threshold below which the money is not worth the effort. Small amounts of friction can have large effects! High overhead means only larger projects will happen. Larger projects take more time and are more serious, so if all projects were large it would kill two critical pieces for getting to breakthroughs: and play. High-overhead, formal grant applications weed out many potentially useful collaborations such as people who don’t understand how the grant process works or who are terrible at writing grants (both of which are unrelated to their ability to do good work.)
The ability to move quickly is important because often the money is going towards keeping the lights on or a grad student in the lab, so if an organization can’t get the money quickly they are going to work on a different project and become unavailable even if the money is available later. Fast money allows a PM which can make it more likely to succeed. There is also something intangible about the feeling of ‘momentum’ that you can’t get if you have to constantly go over road bumps.
Of course, the ability to deploy money quickly requires high trust in both the PM’s integrity and their judgement. Restrictions on spending money happen when you reach trust limits. Overhead exists for a rational reason –money can be embezzled and people always spend money for a purpose so whoever is providing the money wants to know that it is being well-spent. Yet another reason why it circles back to “.”
DARPA PMs have the ability to pull funding built into contracts with performers, which means that they can quickly move money away from an approach that isn’t working and into an approach that is working. You would expect people to be hesitant to work on something risky if they know that the funding could be pulled quickly. pointed out that the actual pieces of the programs are less risky, because within a project the goals can shift.
It’s not clear whether easy fund-pulling was always part of DARPA or if it was introduced as part of formal process around deliverables. However, it seems worth considering part of the ARPA Model and replicating for two reasons.
First, it makes sense that easily re-deployed funds would increase willingness for funding because if you know it’s easy to shut something down it’s easier to start.
Second, it increases the contrast between DARPA and other institutions that give out money like pure grant-giving orgs and venture capital. Organizations that give out long-term grants like the National Science Foundation or Howard Hughes Medical Institute need to either very carefully consider proposals which leads to death by committee or lean on trust in a researcher’s experience. Either way, it slices out a large amount of idea-space. Venture capitalists write checks that are meant to fund a company for 18 months or more. This timescale means that they can end up with a lot of sunk cost in a company that is clearly not doing well. That possibility rationally leads to more risk aversion and when it inevitably happens it can burn time and resources trying to help the struggling company.
Mechanically, DARPA sets up easily-redeployed funding by using contracts instead of grants for most research and having goals in the contracts that are almost impossible to hit. If the performer doesn’t hit the goal, it is at the PMs discretion whether to cancel the contract.
Executing on this framework is different for every case, which is why , able to t. However, it’s still worth going a few rungs down into what this means.
At the end of this step, a PM should have a concrete vision of where the world could go, evidence that ‘on paper’ it doesn’t violate known physics, and a precise list of experiments you would want to do before putting it in front of the tech council and subjecting it to the Heilmeier catechism. J.C.R Licklider’s “” is the classic example of a concrete vision. Tactically, PMs get to this point by first talking to researchers in a domain about what they’re working on and start to synthesize possibilities into a vision of where the domain could go. They also get small groups of researchers together to hone ideas against each other and figure out where the key constraints lie. Massive constraints imposed by the laws of physics can kill the program right there, but if there is uncertainty that can be
At the end of this step, a PM should have demonstration-based evidence that creating the vision is possible and a roadmap for how to get there. The evidence and roadmap . Tactically, PMs get to this point by bringing together small groups of researchers to map out precisely what the pieces of the puzzle look like, which are the most risky, and where the unknowns are, what experiments could be done to resolve the biggest risks. They figure out where you can’t get more precision without experiment and do those experiments as part of seedling projects. The PM lays out where the biggest blockers are along the roadmap and figure out the different approaches that you could take to remove the same blockers.
This is where the PM spends the majority of the time and money in the program and can potentially last through the tenure of multiple program managers. During this step PMs fund different groups to work on different pieces and approaches for the problem. The PM makes sure that the groups working on different pieces are communicating through both formal and informal channels to minimize getting stuck and maximize new ideas. The PMs adjust frequently, killing approaches that aren’t working and reroute funds to new approaches that come up.
Most of this money goes towards small seedling projects. These seedling projects are small grants or contracts designed to help solidify that an idea is both not impossible and that it is in fact possible within scope. Intriguingly, this is in the same ballpark as a large seed round for a startup or the amount of money you need to set up a lab.
According to PMs I’ve grilled on this question, the closest thing to a framework that PMs use to guide program design is “be able to explain precisely why this idea will work to a group of really smart experts both in the area of the program and adjacent to it.” In short, PMs design a program against a mental model of the
The amount of risk the council is willing to give a thumbs-up on depends heavily on the office and its role. The Defense Science Office is much more risk tolerant than the Tactical Technology Office for example. The Tactical Technology Office actually builds prototypes and passes them off to the military, while the Defense Science Office works on more speculative projects.
PMs get throughout the program design process on whether the program is likely to be approved by the council. It’s key that this feedback is from people who are good models of the council as opposed to schmucks with an opinion, which is the case with advice in many other disciplines. I suspect this zero-consequence but tight feedback loop during the design process is important.
While the framework doesn’t have much structure, it does give PMs a very fixed end goal – answering . The testament to the usefulness of The Catechism despite the fact that it wasn’t created until after DARPA had many of its early wins makes me suspect that it is a
The unstructured framework depends on DARPA PMs beingbecause there is almost no explicit guidance and the feedback loop depends on self-motivation. Yet another reason
The Tech Council is composed of people with technical expertise in the proposed program’s area and adjacent areas. The Tech Council Pitch Meeting is meant to be very high level but council members can ask deep technical questions on anything. The tech council doesn’t have any power besides advising the director on the program’s technical soundness. A purely advisory tech council seems like a good idea because it both avoids decision by committee and keeps all responsibility squarely on the director and PM.
PMs should have ‘derisked’ the idea before going into the meeting by using seedling projects, workshops, and precise roadmapping. The way the tech council meeting was described to me is that it’s roughly like a university seminar in a room full of people who you cannot bullshit and who have enough technical experience to dig into anything about the program. It’s important that the meeting be egoless and clearly focused on making the program as good as possible because this sort of thing can easily go down a rabbit hole if people feel the need to show how smart they are or just destroy the presenter. The need for the tech council to ‘get it’ suggests that it should be composed of other PMs.
Seedlings are 3—9 month projects that cost $0.05M to $1M and are designed to “Move concepts from ‘disbelief ’ to ‘mere doubt’”. This means that in an initial exploratory tranche that costs approximately $1.5m, you expect to run roughly a dozen seedlings.
There is little oversight on the money spent on seedling projects as long as the budget is less than ~$500k. PMs don’t need to get the money pre-approved and unlike larger and later projects, DARPA PMs don’t have to use open solicitations for seedlings. In essence the PM can go to whoever they want and say “I need this done.” Zero oversight enables them to move extremely fast. Restrictions on spending money happen when you reach trust limits, so this low-oversight spending is another reason why DARPA depends on high trust in badass PMs.
Seedlings are not about finding a solution to a problem, they’re designed to verify or disprove a hypothesis. The idea for seedlings can either come from the Program Manager or from a performer. Either way the ideas are part of a during program design.
Everybody at DARPA has deep experience in some technical area and there is a culture of people dropping by and asking each other about the subject of their expertise. The way a former PM described this atmosphere was weirdly similar to the one attributed to Bell Labs at its peak. The culture also encourages PMs to discuss their programs with other PMs. This cultural artifact is special because it would be easy for everybody to mind their own business as everybody is working on their own programs. It would also be easy for PMs to feel competitive. DARPA’s small size probably helps walk this fine line between PMs not caring about what other people are working on and caring too much. I’ve read some accounts that disagree with this description of DARPA culture, instead portraying a situation with little interactions between PMs. I attribute the discrepancy to the culture being different either in different offices or at different times because I put higher weight on the description I heard directly from talking to former PMs.
Performers who get DARPA funding are required to share research with each other at various closed-door workshops. Since they are all presumably working on different aspects of the same problem, this seems valuable. The sharing has some of the aspects of but among a much more focused group of people. Ideally, the closed-door workshops bring together the people who might benefit from the knowledge and keep out the tourists and hangers on that can destroy nascent communities. The forced early sharing stands in contrast to normal academia where everything is a first-to-the-post system that incentivizes people to pipet out information to their peers because they are (rationally) worried about getting scooped.
DARPA derisks working on breakthrough ideas for three big groups: researchers, companies, and other funders.
DARPA obviously derisks whether researchers will be able to get funding to work on an idea. Researchers don’t have as much uncertainty around grant proposals because . Instead of the common situation where a funder says “that sounds great! But I need to check with my boss/our budget doesn’t allow it,” if a PM says “that sounds great” it probably means that you’ll get funding. The ability to plan is a big deal. PMs also derisk working off the beaten path for researchers more subtly by building a community around a technological vision. The community is secretly critical because the peer review and citation system incentivizes people to work on things that other people think is interesting. So even if an academic could get funding to work on crazy shit, most people wouldn’t work on it because they wouldn’t be able to get the results published and cited. By , the PM gives researchers peers.
DARPA derisks working off the beaten path for small companies by giving them more confidence that there will be customers for their product –either large companies or the government. In the best case, the promise of future procurement functions like a prize to incentivize startups to spend their own money on top of the money from DARPA. Startups building ‘frontier tech’ often falter at the stage where they need to scale up production. . In this way DARPA PMs act in a similar way to biotech VCs, brokering relationships between small companies with specialized skills and large companies with production capacity. Additionally, other customers often see DARPA funding as third-party validation of a startup’s technology. The DARPA validation can be critical for breaking the chicken-and-egg that nobody will buy your product until someone has bought your product.
From a founder: “DARPA funding has the added benefit of communicating to a third party a validation of the technology.”
For large companies, the off-the-balance sheet work to show that an idea is feasible and clear evidence of demand derisks the idea to the point that they’re willing to start spending their own R&D dollars on it. Companies want R&D to be off of their balance sheets as much as possible. For example, DARPA worked with IBM and Intel to develop nanophotonics and afterward the companies took them on as R&D programs.
“So the DARPA piece, while large, was the validation for IBM to spend their own money.” He continues, “The same way for the Intel piece. You know, Intel certainly looked at that project, and then Intel ended up funding it internally, but the fact that DARPA went back to them three and four times and said, this is an important thing, this is an important thing, you know, it got to the board of directors, and it got high enough that they set up a division to do this.”
Most grant-giving organizations try to derisk them as much as possible9. Previous DARPA funding can give research groups the funding they need to derisk a key part of the technology enough that they can get follow-on funding from more risk-averse grant-giving organizations.
From a professor: “Once you’ve gotten funding from DARPA, you have an issue resolved, and so on, then you go right ahead and submit an NSF proposal. By which time your ideas are known out there, people know you, you’ve published a paper or two. And then guys at NSF say, yeah, yeah, this is a good thing.” He continues, distinguishing DARPA’s place within the broader U.S. government system, “NSF funding usually comes in a second wave. DARPA provides initial funding.” As a consequence, he concludes, “DARPA plays a huge role in selecting key ideas” (from among the broader set of ideas present in the research community).
DARPA analyses can end up looking like hagiographies – this document is no exception. Clearly DARPA has downsides. Instead of caveating every conclusion, it seems productive to group problems thematically and use those groupings to suggest places where an organization using the ARPA Model may be able to improve on the original.
The D in DARPA stands for “Defense” –ultimately DARPA’s explicit purpose is to support the DoD. Even before the addition of “D” ARPA was mission-oriented around the military. at the same time as J.C.R. Licklider was sowing the seeds of personal computing and the Internet, William Godel was managing ARPA programs to build silent planes and boats, agent orange, and AR-15 rifles. Even J.C.R. Licklider’s computer work was started in response to an incident where the US almost started a nuclear exchange because a computer couldn’t tell the difference between the Moon and a fleet of incoming bombers combined with JFK’s desire to have a better command-and-control overview of the US military. For the most part, the non-military technology that came out of DARPA was a happy byproduct.
While we can abstract the ARPA Model away from DARPA’s military focus, it is important to keep that focus in mind because in the long run incentives win and at the end of the day, innovation organizations that are misaligned with their funding source are either neutered or destroyed. Aspects of the parent organization leaks into any innovation organization’s focus regardless of any commitment to paradigm-shifting long-term work.
The military milieu of the day has always driven DARPA’s focus: Vietnam, the Cold War, concerns about offshoring eliminating US ability to build its own military technology, and terrorism. DARPA is the source of many technologies that the show Black Mirror has used to paint dystopian futures – killer drones, surveillance AI, walking robots, and more.
You can see this focus leak in ARPA-E, the Department of Energy (DOE)’s ARPA riff. The DOE doesn’t really have one straightforward mission – it used to be “ensure nuclear superiority” (historical sidenote – all the DOE national labs were originally established to optimize and advance different parts of the nuclear weapons process.) ARPA-E is similarly a bit confused – is it trying to lower the cost of energy? Shift us to renewables faster? Help the energy industry or upend it?
Two upshots. First, DARPA’s military focus means that there are ideas that are out of scope. A former PM explicitly confirmed that while DARPA is ideas limited, there are ideas well-suited for the ARPA Model that DARPA doesn’t pursue. Second, the source of authority and funding matters for anybody attempting to riff on the ARPA Model.
The same mechanisms that enable an organization to move quickly and work on weird, paradigm-shifting programs can also enable massive waste and fraud. The parallel stories of J.C.R. Licklider and William Godel illustrate both edges of the sword. Both men were ARPA program managers in the ’60s. Both had precise, grand visions of technology that could change the world. Both had unmonitored access to funds once the DARPA director gave the ok. But while Licklider helped midwife modern computing and computer science as a field, Godel helped unleash ineffective chemical atrocity on Vietnam, laid the groundwork for the security state, and was arrested by the FBI and convicted for embezzlement.
The experience of working with ARPA is also high variance. Both first and second-hand experience confirms that sometimes DARPA is an amazing partner and sometimes it is hair-tearingly frustrating. Sometimes you come in expecting someone like Licklider and you get something closer to a standard government bureaucracy. Perhaps here is a place where you could actually improve on the model with the modern ‘innovation’ of customer obsession – high quality programs depend on continued relationships with high quality performers, so being a pleasure to work with should be paramount.
Uncomfortably, the ARPA Model’s high variance is a case where you can’t cut off just one tail of a distribution. Any guard rails would slow down the process or constrain PMs, reducing both possible downsides and potential massive upsides. It is unsatisfying but the only solution that doesn’t kill the goose that lays the golden eggs is “culture and good people.” Acknowledging this fact directly enables everybody in an organization riffing on the ARPA Model to look the potential downsides straight in the eye. “With great power comes great responsibility” is a great adage for program managers.
DARPA doesn’t always stick to the ‘ideal’ APRA framework that others and I normally describe. DARPA programs can also look much more like a normal government R&D program – the military needs something, so they tell the director to start a program around the idea. The director finds a program manager to execute on the idea. The program manager ends up looking much more like a project manager with very little input over the direction of the program at all. This way of doing things seems relatively rare and happens more in the military-systems prototype focused offices (TTO and DSO) than elsewhere
While DARPA has been granted some exceptions to broad government rules around hiring and how they can spend money, DARPA is still subject to many ‘stupid government rules.’ They aren’t allowed to use Google Docs or Zoom regardless of how un-sensitive information is. Modern DARPA still requires grants to go through the official government grant application website. The grant application page is almost tear-inducing. Cold contacting a PM requires filling out a web form that then sends a note to the PM’s secretary who may or may not set up a time for you to talk to the PM a month out. I can only imagine this friction reduces the number of serendipitous ideas PM’s receive. The IARPA, the National Intelligence Agency’s ARPA organization, puts emails directly on the website so ‘it’s to prevent too many emails’ is not a valid excuse. From personal experience, at least some DARPA employees treat the weekend as sacred no-work-email time regardless of urgency – a behavior I associate with large bureaucracies where people have little stake in outcomes.
And at the end of the day politics still sneaks in. The biggest example of this were the changes in 1972 thanks to shifting views on the military as a consequence of Vietnam. Throughout DARPA’s history, new presidents have occasionally replaced the DARPA director and starting in 2001, DARPA directors began to sync up with presidential administrations, which suggests increasing politics over time.
The path of least resistance when you’re hiring is to hire people you know, and people tend to know people like themselves. This human tendency, combined with hiring flexibility means that DARPA tends to bring people on as program managers who are already in the DAPRA sphere – researchers who work on government projects, military personnel, and generally “Washington DC people.”
One consequence of insularity is that, from personal experience10, there is a significant cultural gap between DARPA and Silicon Valley. This gap includes legal organizational structures, the expectations of funders, the importance of storytelling, communication style, and more. Since venture capital and startups are an increasingly important technology dispersion mechanism, the culture gap impairs DARPA’s ability to effectively transfer technology. To be explicit: my point isn’t to criticize DARPA for not having more of a ‘startup culture’, but to illustrate that cultural insularity can impede technology dispersion.
Cultural inbreeding can also impede DARPA’s ability to work with the best possible performers. While ideally program managers can cast a dragnet that puts their program on the radar of everybody who might be able to contribute, in reality many people who might be able to contribute are totally unaware. The announcements are still mostly picked up by people in the DARPA “sphere.” I have personal experience with this gap – I was working on technology for manipulating an uncooperative satellite at literally the same time that DARPA was running a program to capture and repurpose satellites and didn’t hear about it until after the grant calls had closed.
There is also a fine line between ‘working with people you trust for the sake of expediency’ and ‘giving money to your buddies even if they aren’t the best ones for the job.’ Although PMs have definitely gone over this line – the Total Information Awareness program poured money into a consulting firm run by the PMs former colleagues – DARPA has managed to remain shockingly scandal free.
A riff on the ARPA Model could possibly address the potential inbreeding problem explicitly putting in effort to seek out weirdos and people from ‘different worlds.’
The ARPA Model has the explicit intention that technologies get out of the lab and into the real world. Clearly DARPA has successfully transitioned paradigm-changing technology to the government, large companies, and startups, so the model’s design isn’t worthless. However, many DARPA technologies still fall into ‘The Valley of Death’11 and even successful transitions often are not smooth.
DARPA’s history pockmarked with stories that go “and then at the end of the program, the military or industry said ‘that’s cool, but we like the way we do it now.’” Or perhaps worse, they say ‘that looks great’ and take ownership of the technology but then completely stop working on scaling it up. In some of these cases the outside organizations come around: DARPA funded the development of UAVs in the ’80s, the Navy took on and then killed the program, DARPA continued development until the military paradigm shifted in the ’90s. The story is similar for optoelectronics. While counterfactuals are hard, these common ‘near death’ stories suggest that there are many programs that vaporized on impact with existing paradigms.
Each transition failure, like unhappy families, is unique. Some of the failure modes do rhyme:
Many of these failure modes illustrate the tension between ‘building something people want’ and ‘building something capable of shifting paradigms.’
Transitions are an area where an organization riffing on the ARPA Model may be able to make big improvements over DARPA. It is important to first acknowledge that DARPA doesn’t exist in a vacuum. The mechanisms for technology dispersion at its disposal are subject to the constraints of the world around it. In the 1970s that meant large corporations like Xerox, defense contractors, or government labs. The constraints on those organizations have shifted, and VC-backed startups have become an important mechanism as well. DARPA has worked to adjust to this new environment – going so far as to create a commercialization team in 2017. But from personal experience the adjustment has been clunky. I don’t have a great answer yet, but it’s important to ask “what would an organization built from the ground up with transitions into today (or tomorrow’s) environment in mind look like?”
When talking about riffs on the ARPA Model, it’s important to distinguish between organizations that spiritually riff on the ARPA Model and structurally riff on it. Spiritual riffs (or just spiritual rhymes) are organizations that have enabled or strived to enable high-risk, possibly paradigm changing, goal-focused research. People often conflate DARPA with great R&D organizations of the past – Bell Labs, Xerox PARC, Lockheed Skunkworks, and others. It doesn’t help that DARPA funded and helped organize research at all of these places. While I am all for being spiritually inspired by DARPA, we’re digging into the hypothesis that DARPA’s structure is worth riffing on, so I’m going to ignore organizations that fall into this category.
To my knowledge, there haven’t been any attempts to structurally riff on DARPA before the latter half of the ’00s. This timing is intriguing in itself, and a pure speculation is that it is the consequence of a dawning realization that something wasn’t working in the research pipeline. But that is another story for another time. Evaluating these ARPA rifflings as successes or failures is difficult, given that they are all younger than 13 years old, ARPA style programs usually take five or more years to produce a result (and often much longer to have an impact), and the expected success rate is 5—10 programs out of every 100. I will touch on whether they ‘feel’ success-y, but primarily we should focus on the deviations they have made from the standard ARPA Model, whether they make sense in context, and whether we would expect the deltas to lead to more success or failure over time.
There are surprisingly few attempts to riff on the ARPA Model. The US government has built two DARPA imitators: IARPA and ARPA-E. The British government has floated building an ARPA. In the private sector, Google ATAP is DARPA-esque enough to talk about and Wellcome Leap appears to be a full-on health-focused implementation of the ARPA Model.
I(ntelligence)ARPA started operation in 2007 and is run by the Department of National Intelligence. It currently has 17 program managers as of 2020, which makes it roughly the size of one of DARPA’s six offices. At first glance, it has all the pieces of the ARPA Model: empowered program managers coordinating high-risk high-reward external research.
IARPA explicitly does zero commercialization – all technology transfers are to intelligence agencies. This stands in contrast to DARPA which transfers to large companies and the VC/Startup Ecosystem as well as DoD agencies.
IARPA spends around a quarter of its budget on testing and validation of the technology that comes out of its programs. Given IARPA’s focus on computer security and computation in general, this spending both makes sense and is intriguing. What would a focus on testing and validation look like for other technologies? One failure mode for technology trying to leave the lab is extreme fragility (only working in ideal situations, etc.) and a validation mechanism might cost more in the short term but lead to more robust technology in the long term.
IARPA uses contests and tournaments as a first-class tool for generating research. DARPA has run a few tournaments which arguably were significant successes – the grand challenge and the urban challenge catalyzed a phase change in autonomous driving from a research novelty to a potential industry. The DARPA robotics challenge was disappointing, but ⅔ is great for high-risk programs. Despite the outlier results, DARPA tournaments are the exception, not the rule. The reasons for this difference aren’t clear – it may be that computing-based tournaments are easier to coordinate and standardize or it simply comes down to a matter of culture. Several economists have pointed out that prizes are underused as a research funding mechanism and when I’ve directly asked DARPA PMs why they don’t use prize mechanisms more often the answer was “I don’t know.” IARPA’s regular use of tournaments, DARPA’s infrequent but high impact tournaments, and missing evidence to the contrary suggests that prizes may be a useful place for an organization riffing on the ARPA Model to explore.
Surprisingly IARPA is much less sensitive about its research than DARPA. Most of IARPAs programs are unclassified, in contrast to ~1/3 of DARPA programs that are classified. IARPA also funds organizations outside the US. It seems useful to tap into as many resources as possible so my hunch is that this is a useful change.
IARPA has a policy of making sure there is a potential intelligence agency ‘customer’ before undertaking a program. While this seems well-intentioned, it means that IARPA will never be able to change a paradigm unless an intelligence agency already feels like it should be changed.
IARPA has 37 ongoing programs and 26 completed programs as of mid 2020. At a 10% success rate, there’s a 95% chance that at least one of them would have succeeded.
IARPA funded a significant chunk of quantum computing research in the US in the 2007-2010 period, including David Wineland’s research that went on to win the Nobel Prize in physics in 2012. It’s not completely roses though – IARPA cut off funding to NIST researchers, including Wineland, because they didn’t want to fund other government organizations. It’s not clear if they resumed that funding or are claiming credit for the Nobel prize research that they funded and then cut off …
“As of 2009, IARPA was said to provide a large portion of quantum computing funding resources in the United States.”
Has IARPA started any industries yet? No, but if quantum computing becomes as big a deal as people think it could be, I suspect IARPA will play a large role in the stories about it.
Not serious note. Look at this list of IARPA program names and rejoice ye LoTR and Mythology nerds: Ithildin, MAEGLIN, SIMARILS, Amon-Hen, Odin, ATHENA, ICArUS, Mercury.
ARPA-E(nergy) started operation in 2009 and is run by the Department of Energy. It currently has 20 program managers and a budget of ~$180M as of 2020. That makes it approximately the size of one DARPA office. Like IARPA, it has all the pieces of the ARPA Model on paper: empowered program managers coordinating high-risk high-reward external research.
ARPA-E is on the opposite end of the transfer spectrum from IARPA: while IARPA only hands off technology to its funding departments, ARPA-E primarily targets private companies to adopt and scale up its program’s output (DARPA does both.) Transfer via commercialization makes sense given that the Department of Energy doesn’t actually build or deploy energy technology. ARPA-E adapted the ARPA Model to target commercialization in several ways: it has a whole commercialization team; on-staff lawyers; and explicitly considers how the technology is going to be implemented by the energy industry before embarking on a program. While these adaptations are logical, they may be shooting the ARPA Model in the foot. The additional apparatus around commercialization makes ARPA-E less flat than DARPA – there are more non-PM staff than PMs, which cuts into the benefits of DARPA being tiny and flat.
While DARPA is funded by congress as part of the DOE budget, the DOE funds ARPA-E programs directly. Direct program funding means that the DOE has much more say over which programs ARPA-E runs and how they spend money. This subtle difference in funding sources make ARPA-E less independent from the DOE and may invalidate the buffer between the government political machine and DARPA provided by opacity and its director. Since ARPA-E is targeting transfer to non-DOE entities, the increased DOE oversight may lead to one of those lovely situations where an entity with no skin-in-the-game has a large say on risky activities.
ARPA-E is explicitly metrics-driven. While this approach certainly jives with modern sensibilities, my hunch is that metrics can hamstring embryonic technology. Metrics are great when you know what you’re optimizing, but tend to cause the streetlight effect – you optimize for things that can be measured. Do you know what you’re optimizing when you’re still figuring out how a technology works and what it is good for? What would Licklider’s metrics have been for a personal computing program? It is possible that energy has so few relevant metrics that a metrics-driven approach doesn’t cut down on trying weird things, but I’m skeptical.
ARPA-E is not process-light. I have heard first hand accounts of inflexibility around hiring “despite most of the work being in different parts of the country, you must be full time and in Washington or you will not be invited to all the meetings” and tools “you must use the government issued laptop for everything.” This inflexibility goes against the conclusions that you should pay attention to DARPA’s informal process and ignore formal process and that DARPA is incredibly flexible with who it hires to be program managers.
Most reports about ARPA-E’s impact stress the number of projects they have funded and concrete outcomes are conspicuously absent. It feels like a dog-that-didn’t-bark type situation. The closest to an outlier result was funding the research that led to a solar-cell company named 1366 hitting 19.6% efficiency.
ARPA-E is also operating in a brutal area: the energy industry is notoriously conservative partially because it is behooven to many stakeholders: various kinds of investors, governments, customers, and non-customer residents in the areas where the energy company operates.
Many countries have a military R&D organization that reporters occasionally refer to as “The DARPA of X” (for example Israel’s DDR&D: Directorate of Defense Research & Development or Singapore’s Defence Science and Technology Agency (DSTA).) These organizations do work on advanced military technology but run their own labs and have the military as a more direct customer which makes them closer to Lockheed Skunkworks than DARPA.
Regina Dugan, a former DARPA Director, explicitly organized Google Advanced Technology And Projects (ATAP) to riff on DARPA’s structure. ATAP does high-risk high-reward program-focused research that isn’t afraid to explore new phenomena but leaves out empowered program managers and externalized research. These two missing components make it hard to consider it a true riff on DARPA. It’s much more akin to a skunkworks.
The Wellcome fund – a British foundation dedicated to funding health research – announced a new division called Leap in May 2020. From the scant information available online, Wellcome Leap seems to be organized around empowered program managers coordinating high-risk high-reward external research. From what I can tell, this is the closest a private entity has come to the platonic ARPA Model, at least on paper. There are reasons for both optimism and skepticism about its potential outcomes. Its CEO, Regina Dugan, is a former DARPA director (who incidentally started Google ATAP.) Leap is nominally acknowledging that its programs will take time to come to fruition and have a high chance of failure. Hopefully, the things it has going for it will not be impeded by starting too big: it has a large ($300m) pool of money from day one.
As of mid-2020 there has been a lot of talk about a British ARPA but not much apparent action. Dominic Cummings, Chief Advisor to the British Prime Minister, has written about a British ARPA many times and the Queen’s speech at the end of 2019 featured the idea. Many people have weighed in online and the government is soliciting information about how it might work. That may be a red flag for an organization based on the idea of individual empowerment and non-consensus approaches.
The dominant paradigm of starting an org is to do internalized R&D unless you’re a government or charitable foundation. In reality, R&D orgs lie on a spectrum between externalized and internalized, with DARPA on one end and Lockheed Skunkworks on the other. Externalized research entails working through grants and contracts while internalized research is doing everything in house. There’s nothing inherently wrong with building a Skunkworks – it just means that there are different tradeoffs and the statement “DARPA for X” is misleading.
DARPA started off small and informal. For years it was less than ten people.
Starting too big often causes heavy process. People always spend money for a purpose, so the more money there is up front, the more expectations there are attached to it. One failure mode is that funding entity doesn’t trust a low-track record organization and requires heavy process to create assurance that the money will be well-spent.
Starting large makes opacity hard, and . Starting large with large expectations and scrutiny makes it tough to execute on things that seem stupid. A spotlight also encourages organizations to work on things that seem sexy which makes it hard to generate true outlier output. Remember: if you know it’s easy to shut something down it’s easier to start and the opposite is true as well.
Culture and trust takes time to build. A large organization either needs culture and trust or process to keep everybody aligned so if you start big without heavy process it will just lead to a shitshow. As far as I can tell, this point and the previous one is roughly what happened with.
Regardless of size, directly copying all of DARPA’s processes leads nowhere good. Many of the processes were built up over years to fit DARPA’s exact situation, and as noted earlier, you should
“There is not and should not be a singular answer on ‘what is DARPA’—and if someone tells you that [there is], they don’t understand DARPA”
—Richard Van Atta
It’s important to lay the changes out and discuss whether or not they affected the change in DARPA’s outlier output. Interestingly . The biggest change happened when . Which raises the question: “was the shift from ARPA to DARPA a focus change or a process change?”
It’s tempting to throw out anything introduced since 1972 unless it was a codification of a previously implicit rule. However, the world has changed since 197212 so it’s worth considering whether some adjustments were made to enable DARPA to more effectively operate in the world.
The first elephant in the room is DARPA’s history. Just looking at the for wildly impactful technologies, the difference before and after 1972 is pretty stark.
Before ARPA became DARPA in 1972:
It raises the question of whether there is anything to be learned from the modern organization or whether we need to go completely off of historical accounts. Some of the post 1972 creations are still pretty significant – both autonomous cars and voice technology arguably haven’t reached their potential yet. Additionally, we can attribute a chunk of the perceived outlier dropoff to . While DARPA, most of the changes were changes in official process so if we , there are still valuable things to be learned from post-1972 DARPA.
The expressly limited ARPA funding to direct military applications and gave Congress more oversight into their spending. The amendment was part of broader attitude changes both inside the government and outside of it. Inside the government there was increasing discomfort with how ARPA Program Managers could spend money on basically anything they thought was worthwhile. Unfortunately, you can’t cut off just one tail of a distribution so these constraints definitely reduced the variance of DARPA results, both positive and negative. One might think that the technologies are so broadly applicable that smart program managers could work on anything under the umbrella of ‘defense’ but from talking to former program managers, there are definitely DARPA-style ideas that DARPA doesn’t pursue because they are not sufficiently defense related.
The economy also tanked in 1973, which contributed to Congress being more concerned about what they were getting for their money. They didn’t want program managers like J.C.R. Licklider prancing around spending money that didn’t have a clear payoff. This historical note emphasizes the point that to pull off long term projects, innovation orgs need to be aligned with their money factory so that they’re not dependent on fair weather funding – sources of money that flow only when the economy is good or they’re working on something popular.
Outside the government, popular opinion turned against the military in the early 1970s, which both put pressure on elected officials and changed attitudes towards working with ARPA. The change in opinion made university researchers more hesitant to take military money. It also may have made fewer high quality people want to join the org, which arguably probably persists now. The stigma around working for the military puts additional weight on the question of s?
Together these raise the question ...
The transition from ARPA to DARPA involved both a focus change to explicitly military projects and more formal process and oversight. Since most of DARPA’s outlier output happened before 1972 the shift raises the question of whether the output dropoff was more a function of the change in DARPA’s process or its focus. There are arguments for both ends of the spectrum.
The process argument is that after 1972 oversight and increased friction killed DARPA’s ability to create outlier results. Both increased demand that programs have a waiting customer and increased spending scrutiny embodied by things like The Heilmeier Catechism and the Tech Council hamstrings program managers. This argument definitely has merit because small amounts of friction can have large effects and you can’t cut off just one tail of a distribution.
The focus argument is that we just don’t see or appreciate as many of the things that come out of DARPA because they are specifically for military use and have less broad applicability.
The focus vs. process question is important because it determines whether there is anything to be learned from how DARPA works today. If the changes in process that occurred after 1972 are the direct cause of the drop-off in outlier output, then analyzing the DARPA process today is worthless. If the focus shift caused the drop-off in outlier output, lessons from today’s DARPA remain valuable. In reality, it is probably a mix of both.
The visceral excitement that comes out of (recent) former program managers when I’ve talked to them about their time at DARPA suggests that there are many things to be learned from the current organization that is not just cargo culting. At the same time, the majority of changes to DARPA over time have involved adding more explicit process. How can we resolve these two ideas? I would suggest that the solution is to
One non-focus, non-process reason for the change in outlier output may be that DARPA can’t attract as many amazing people because they have better options or don’t want to work on explicitly military things. If this were the case, it would severely affect output . However, there are still super high quality people in DARPA so this cannot explain all the changes.
For the most part there’s been few changes in the weird things about how DARPA’s program managers work compared to other organizations, the incentives and structure of the organization, the funding, and general shape of the process. So it is not worthless to study the modern organization. Regardless of whether or not the are the reason that , they certainly didn’t help. Therefore, if you want to replicate DARPA’s outlier success, it makes sense to pay attention to DARPA’s informal process and ignore formal process.
Usually, formal process is put into place to increase oversight and decrease reliance on trust. Formal process lets people outside the organization trust in the process instead of the people. Ignoring the formal process makes the success of an organization depend more on trust in people.
This trust-dependence means that it is essential for an organization that seeks to replicate DARPA’s success to start with trust from funders and collaborators outside the organization. The trust-dependence creates a chicken-and-egg situation because by definition new models and organizations do not have a track record and the people who are most likely to create a new game are ones who haven’t won at other games.
DARPA doesn’t do any research in house, which has several advantages. However even in the domain of mission-focused research examples like Lockheed Skunkworks, Bell Labs, and others have demonstrated that internalized research can produce excellent results and has clear advantages. Internalized research lowers some set of transaction costs, enables closer collaboration between disciplines, smooths transition to manufacturing, and makes capturing value easier. The fact that internalized vs. externalized work is not a binary distinction but a spectrum complicates the situation. My hunch is that there is some class of work where the advantages of externalized research dominate and another class of work where the advantages of internalized research dominate. I don’t have a good answer to where that line is, but it is an important question to address.
DARPA is a small fraction of the Department of Defense Budget. Similarly, other storied research organizations tend to be attached to large ‘money factories’ and represent a small fraction of their budget—at its height, Bell Labs’ budget was only 5% of AT&T’s revenue. By contrast, my sense is that even well-capitalized independent research-focused organizations feel constant pressure that can impede long-term research efforts. Now, plenty of corporate labs produce nothing of note, so being attached to a larger money-making organization is certainly not sufficient for producing long term results. It’s important to understand whether that money factory is necessary.
Prizes seem like they could be a natural fit with the ARPA Model, yet DARPA doesn’t seem to use prizes outside of a few examples like the DARPA Grand Challenges and Robotics Challenges. Specifically, prizes seem like they’re just one more path along the theme of top down problems and bottom up solutions beyond open solicitations and parallel projects. IARPA’s heavy use of competitions suggests that the question is worth asking. One prize-dissuading possibility could be that most DARPA projects are more capital-heavy than IARPA’s mostly computer-based-projects and capital requirements would make people hesitant to work towards an uncertain payout. Another possibility is simply tradition and government rules. It’s worth knowing whether it’s the former, the latter, or something else if you’re going to riff on the ARPA Model.
Successful big things usually start small and many attempts to replicate DARPA’s results start too big. So it makes sense to ask: can you start with a tenth of DARPA’s budget? A hundredth? A thousandth? There are two lower budget bounds that you’ll run into: the number of parallel high-risk programs you need to run to get a success and the budget per program to have a viable shot at that success.
A back of the envelope calculation suggests that if each program generously has a 10% chance of success then you need to run at least seven programs to give yourself a 50% chance of at least one program being successful.
The question of minimum program budget is trickier. Let’s look at some comparison numbers. In the years 2018–2020 among DARPA programs not focused on assembly and production the minimum budget was $2m, the maximum budget was $31.4m, and the average budget was $12m. The ARPA IPTO directorate that midwifed the personal computer started with a budget of $47m in 2020 dollars. ARPA-E vacillates between ~$200–300m/year and has about 50 programs running at any time, which comes out to roughly $4–6m per program. IARPA’s budget is classified. Could a program go below a couple million dollars a year and still be effective? There are arguments both ways. On one hand you could argue that surely bureaucratic inefficiency is pushing those budgets higher than they need to be. On the other hand, it might be that the sort of work most valuable for an organization riffing on the ARPA Model to undertake needs a relatively large budget, otherwise it would be picked up by other funding mechanisms.
A large part of a DARPA program manager’s job is focused network building and the Internet is one of the greatest network building tools of all time. However, DARPA doesn’t have a strong web presence and the idea that DARPA’s aversion to people with a web presence may be how they avoid asymmetric career risk suggests that there are good reasons for the low Internet utilization. However, the Polyplexus project, a DARPA effort to foster an idea-generating online community, suggests that DARPA may realize that it’s no longer at the pareto front of this tradeoff and that it might be able to more effectively use the Internet to execute on its model. The Internet could conceivably help PMs find people working on the edge of a space, foster communication between performers, and find gaps in the state of the art. What would a riff on the ARPA Model built to take advantage of the Internet look like?
The Advanced Research Projects Agency model is of an organization set up to maximize the agency and effectiveness of (PMs) who coordinate to midwife technology that wouldn’t otherwise happen (Programs.)
The , but has still produced over time so with . PMs need specific characteristics to succeed: , , vision, and ability to act under uncertainty. PMs also need to be because the model depends on their ability to and . These PMs have , which enables , aligns incentives, and enables it . It’s worth deeply because they are
Organizationally, DARPA is, and . It is set up to through. . DARPA’s . On top of many tacit tools, PMs execute on these steps by and before presenting a program design to .
DARPA provides a critical ‘in-between’ role in the world. It cross-polination and derisks for both .
The number of interlocking pieces is huge but this breakdown should give you hope – none of these admonitions are magical or depend on irreplaceable configurations of people in time. Riffing on DARPA will be incredibly hard. ‘DARPA hard, perhaps?
As I noted , the entire point of this document is to inform action. This is not the place for a deep dive on what those actions could and should be but I wanted to leave you with some sketchy questions and considerations for replicating DARPA’s outlier success that I plan to tackle.
The first question, of course: “is it worthwhile to riff on the ARPA Model?” Yes. It’s notable that in conversations with former PMs, they explicitly noted that there are many program ideas that are shelved (and often forgotten) because they fall outside of DARPA’s military-focused scope. If anything we need it now more than ever.
Does an ARPA need to be a government organization? Is it possible to create a private ARPA? Nothing suggests that it’s impossible, but there are several pieces that need to be figured out first.
Some uncomfortable truths:
A big consideration for anybody hoping to emulate DARPA’s success outside of a government agency is the question of ‘how will money work?’ The ideal situation would be for the organization to be its own money factory, but it might be impossible to accomplish that while preserving the structurally important pieces of the ARPA Model. Another huge consideration is how to set up incentives both to work with high quality PMs and for potential performers in big companies, small companies, and academia to take you seriously. These considerations suggest that replicating ARPA’s success outside of a government might require truly new organizational structures.
There are also exciting places where it may be possible to riff on the model. Building more structured roadmapping frameworks could make program design even more effective. You might be able to build trust during the program design period by having potential PMs do a ‘residency’ instead of making an upfront binary decision. It’s even possible that program design and execution could be decoupled. You could seed even more awesome if another organization is willing to execute on the program after it’s been derisked by showing that it is both not impossible and is in fact possible. These are just a few of the possibilities! If you want to work with me on the second step, or just
So many thanks to the people who gave well-thought out feedback and encouragement on this: Andy Matuschak, Sam Arbesman, Martin Permin, Rebecca Xavier, Jason Crawford, Luke Constable, Mark McGranaghan, and Cheryl Reinhardt. Thanks also to Mark Micire, Anna Goldstein, and Erica Fuchs, Michael Goldblatt, and others for letting me ply them with many annoying questions.
The styling and interface of this website is mostly derived from Andy Matuschak and Michael Nielsen, “How can we develop transformative tools for thought?”, https://numinous.productions/ttft, San Francisco (2019)
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