While building PARPA, I’ve run into many pervasive beliefs about intrinsic motivation in research, research management, and the role of funding organizations in both. While I’m hesitant to say that they’re wrong, I do think there’s a lot of room to upgrade how we think about those things. 

Let’s start with two pieces of accepted wisdom about research that often find themselves in tension. (If you buy both conclusions, feel free to skip this part!)

#1: Great Research requires intrinsic motivation

There are three core reasons why great research requires massive motivation:

First, great research hinges on people thinking about problems all the time: from Archimedes realizing that buoyancy came from displacing fluids in the bath to Kary Mullis’ famous night drive where the idea of PCR came to him.. These discoveries require questions to be constantly percolating in the back of your mind. 9 to 5 just doesn’t cut it.

Second, great research often requires risks to reputation, careers, or physical wellbeing. Newton stuck a rod into his own eye to experiment with how lens deformation affected vision. Edwin Land had to break and enter as part of creating the polaroid process: climbing through a window via a 6th-floor ledge in order to use a Columbia lab’s powerful magnet.

Third, researchers on the knowledge frontier are often ridiculed, scorned, or persecuted: both from within their communities or outside of them. [1]

The timescale of glory, even for successful research, is often tens of years, if not lifetimes. Add that to the fact that the goal of great research is rarely to become rich and it’s clear that a good chunk of that massive motivation needs to be intrinsic.

The importance of intrinsic motivation has created a common perception (both among researchers and non-researchers) that the ideal state for doing research is, as Vannevar Bush bush put it in “Science, The Endless Frontier”:

Free play of free intellects, working on subjects of their own choice, in the manner dictated by their curiosity for exploration of the unknown. 

But at the same time …

#2: Research management matters

Most researchers bristle at the idea of being managed. But management happens all the time in research, from academic labs to CERN. Nobody likes the idea of being managed, but many triumphs of research, especially in the 20th century, depended on good management.

At some point, unless the work for a project can be done by a single person, someone needs to play a coordinating function. As uncomfortable as it is to say, coordinating involves getting people to do things they wouldn’t do otherwise. Successful research organizations from LIGO to DARPA to any academic lab with postdocs and graduate students have leaders nudging people to do more of some things and less of others. These nudges can be at various levels of abstraction and involve various levels of coercion, but at the end of the day, coordination involves getting two or more people to work together in a way they would not otherwise do. In other words, research management matters.

But isn’t it a bad idea to tell people what to do if great research requires massive intrinsic motivation? 

This tension, I think, is resolved by two facts: context affects the types of ideas people have and the work they do to pursue those ideas and management isn’t just telling people what to do. 

 

Context affects the types of ideas people have and the work they do to pursue those ideas 

Context plays a large role, not just in what people think is important, but for the sorts of ideas people have in the first place. Context is a frustratingly nebulous term that I won’t even attempt to circumscribe. When thinking about research ideas, there are two key aspects of context that are worth focusing on: the culture someone swims in and the resources that they believe to be at their disposal.

I want to make a sideways argument about research ideas by talking about startups. It’s a world where success demands similar levels of motivation but has some clear natural experiments around the effect of context on ideas. The combined effects of Paul Graham’s essays and Y Combinator (YC) on the startup world is an example of the power of culture and resources to affect the ideas people have and how they pursue those ideas. Paul and YC did incredible work to make starting a startup feel possible for many people around the world. Before YC, there wasn’t some fixed number of people with startup ideas who needed permission and resources to act on them. Instead, there were many people for whom the idea of they, themselves, starting a company had not once gone through their minds. But once the process of creating a startup was legible, they had a community, and they saw the availability of early resources for pursuing that path, then they had startup ideas. The institutions of Y Combinator and Silicon Valley as an idea more generally made previously unthinkable ideas thinkable.

I’m not making a John Locke-ian argument that people are just Tabula Rasas imprinted by society. People had startup ideas long before YC, Sequoia Capital, or even the ideas of venture capital or “tech startups” were minted. But I do suspect that people had many fewer startup ideas before those institutions existed. Furthermore, those earlier ideas were not necessarily the best startup ideas or the ones that people were the most intrinsically motivated to pursue. The context shift did more than just encourage slightly worse or less intrinsically motivated people to pursue slightly worse ideas. There’s no way to prove it, but I suspect that without the context of 2010’s Silicon Valley, top founders with amazing ideas would have just gone down different paths. Context does more than just lower some threshold on an underlying distribution — it changes that distribution.

The ability to change that idea distribution is the mechanism behind Tyler Cowen’s observation that raising others’ ambitions is such a high return activity. Raising someone’s ambitions is often not a matter of simply encouraging them to pursue an idea of theirs that they wouldn’t otherwise pursue. Instead, it involves seeding the meta-idea that they should be pursuing an idea that they haven’t yet had and could pursue it by going down a path that they could not previously conceive. You change the person’s context by providing a new, nebulous combination of what they should do and what they could do.

In a world where people invent things in their basement and then bring them into the world by patenting and selling the rights, people are going to have a lot of ideas about inventions and you’ll see a lot of filed patents. In a world where people create collective action by forming small social clubs, you’re going to see people with a lot of ideas for social clubs. In a world where people start startups, you’re going to see a lot of startup-shaped-ideas.

Focusing back on research: in a world where research is funded through broad grant calls to PIs for them to pursue specific projects where the the majority of work is done by grad students and which are judged on their scientific contribution and publication record, you’re going to see a lot of ideas that appeal to broad grant calls that can be done by grad students that are seeking publishable scientific contributions. People will be intrinsically motivated to pursue these ideas! The ideas won’t be corruptions of researchers’ “true” motivations, they’ll just be downstream of context: the culture that researchers swim in and the resources that they believe to be at their disposal.

 

Management isn’t just telling people what to do

Robert Oppenheimer was Einstein’s manager at the Institute for Advanced Study. Did Oppenheimer tell Einstein what to do in any way? Of course not. He was freaking Einstein! 

Good managers give people who do well with autonomy a ton of it. You might say that these managers aren’t actually managing. But it is management if granting that autonomy is a choice they’re making. While management isn’t just telling people what to do, management does mean that there is always the potential to constrain autonomy. This potential to constrain autonomy is more acute the more someone needs additional resources to accomplish their goals beyond what they control directly. The more resources someone needs beyond what’s between their ears and in their bank account, the more the person providing those resources is managing that person, even if that management consists of nothing but handing over the resources, no questions asked.

However, there are many other knobs that managers can turn and roles they fill besides being simple arbiters of resources and autonomy. Making sure the right people talk to each other, nudging towards more productive paths, setting goals, and giving a group of people a sense of what is celebrated are just a few of the moves managers have at their disposal. (I realize that this is pretty germaine, but people often seem to forget or ignore it in the context of research.) Research management is, in fact, part of the research process itself.

 

Enter funding organizations

Taken together, the role of management in the research process and the potential for context to alter the ideas that drive great researchers leads to a surprising conclusion: funding organizations are not exogenous to the research process.

From the National Science Foundation to large private philanthropies to an individual running a microgrant program, most people default to the view that organizations who give other organizations money to do research are exogenous to the research process. That is, funding organizations are drawing from some stationary idea distribution. They anoint some projects and condemn others to resource starvation and death, but those ideas arise in the world independent of how funding organizations act. 

To the contrary, funding organizations are managing research whether they realize it or not. People consciously or subconsciously shape their projects and agendas to what they think can get funded. Over time, shaping projects around funding affects intrinsic motivations themselves and even the trajectory of whole fields.

Funding organizations’ implicit research management plays out everywhere. For example, many government grants prioritize spending on grad students over equipment, resulting in a paucity of research that requires new equipment and entire fields dominated by experiments that require a lot of cheap labor. I suspect that (in addition to the fact that there is a lot of hype and room for discovery) many talented researchers find themselves deeply interested in biology (especially related to health) and AI because of how relatively easy it is to get projects funded in that area. People think of ideas that look like high-growth startups, discovery-based research, or individual projects not in small part because that’s where the money is. Adam Marblestone has pointed out that the mere existence of Focused Research Organizations as a new funding structure has led to people thinking of ideas that wouldn’t even have become conscious previously.  

If I’m right that funding organizations (and the people who work there) manage research, the question “how do you do research management well?” is understudied. Most discussions of research management seem stuck at “Freedom good. Constraints bad.” There’s certainly some truth to that, but what about questions like “how do you decide who to give that freedom to?” or “what happens when more than one person needs to coordinate in a way that isn’t 100% aligned with their own interests?” I’m still actively learning, but one useful way I’ve found to think about research management is along two axes that lend themselves to a nice consultant-y 2x2: active constraints and opinionatedness.

 

 

Active constraints are the extent of management’s intervention in the research process once a project has begun. This intervention can be anything from demanding reports to sitting down at the bench and pipetting themselves. In completely unconstrained research, once the work is started, management does not intervene. This truly hands-off approach is embodied by how Donald Braben ran BP’s venture research program.[2] If a researcher Braben was working with wanted to take the money and do something completely different than what they initially said they would, so be it. 

A quick aside: Does Braben’s approach even count as management? Disappointingly for those of us (everybody?) who just want people to throw a bunch of money at us and leave us to get on with our work, it does. While Braben didn’t put constraints on researchers once they were in the program, nor did he impose his opinion on which direction they should take, he did have a set of criteria[3] by which he filtered the researchers he invited to the program. He was still creating a context around what research was encouraged and what was not. But what if the criteria were simply a necessity imposed by scarce resources and given infinite resources, the Braben approach becomes “give every researcher the money they want, no questions asked” (which is actually not management)? I can’t read his mind, but everything I’ve encountered that he’s said and written suggests this is not the case. He does have strong opinions about what mindsets lead to good research and wants to encourage people with those mindsets. He wants to create a specific context.    

In a stark contrast to Braben’s hands-off approach, Elon Musk’s style is a good example of active constraints. The Muskian approach to active constraints is exemplified by his management of the Tesla autopilot team: he was directly involved in decisions about hardware and algorithms, firing a big chunk of the team when they weren’t making satisfactory progress. 

Most government granting agencies sit somewhere in between Braben and Musk. They constrain, to some extent, how money can be spent and require progress reports, but steer clear of nitty-gritties and allow some directional shifts as long as they’re still within scope.

Actively constrained management requires more intuition around the work being done.[4] This requirement creates a tricky situation because the people with the best intuitions in a research area usually are some of the best researchers in that area. As a result, more active management requires convincing the best people in an area to be managers. In order for that to happen, those people need to believe that being a manager will advance their research agenda more than other options, creating a tricky problem when an area needs tight coordination to advance but the only people who are skilled enough to do that coordination don’t want to play that role.[5] 

Opinionatedness is how opinionated management is about the research work to be done. J.C.R. Licklider had a clear vision of what human-computer synthesis would look like.[6] He brought only people who shared that vision into his ARPA program that would lead to most of our modern personal computing paradigms. George Heilmeier, another legendary research manager, had a very different approach from Licklider despite being the director of DARPA while Licklider was a program manager there.[7] Indeed, the two clashed so hard that Licklider quit. As long as PMs could answer his famous catechism, Heilmeier had few opinions about what specific work should happen as long as it was broadly in the scope of National Defense.

Together, the research management styles of Braben, Musk, Licklider, and Heilmeier form the four quadrants of a 2x2. Each of them managed research to great success: there are Nobel prizes and iconic technologies that would not have existed without each of them. Yet, their management styles are diametrically opposed. From this, I feel compelled to conclude that each of their approaches are effective for different flavors of research and different sorts of work. Enabling diverse flavors of research – from deep curiosity-driven explorations of how the world works to coordinated systems research – depends on diverse research management approaches and, by extension, diverse approaches and levels of involvement from funding organizations. This conclusion is painfully abstract and incomplete. It raises much more important questions like:

What are the different kinds of research? 

Which management styles work best for which kinds of research? 

Can we know what kind of work an idea needs and what the right management approach is a priori?” 

I will punt on answering them for now because answering them well is a research program unto itself.      

 

 

As an exercise, I tried mapping current institutions onto the constrained–opinionatedness axes to see which flavors of management are more or less represented. Opacity is roughly meant to correspond to how many organizations take a specific approach. My particular mappings are hand-wavy and inaccurate but I will stand by the two broad facts that there are large swaths of open space and heavy representation by both grants and small, tightly-coordinated orgs.[8] Types of research that mesh well with management styles in the heavily represented areas are not only more likely to succeed, but act as basins of attractions for people’s intrinsic motivation. 

 

In summary

Research management matters BUT it doesn’t mean just telling people what to do.

Intrinsic motivation is critical for great research BUT it is malleable.

As a result of #1 and #2, funding organizations are part of the research process, whether they like it or not.

There is no “correct” way to manage research: different management styles push different sorts of research.

Current funding organizations cluster heavily around a few management styles, warping the research ecosystem at the level of intrinsic motivations. 

These points offer several ways to upgrade how we think about funding and managing research and potentially point to areas where there are gaps in the management ecosystem.

 

  1. ^

    Obviously not all great research requires 24 hr obsession, massive risks, and pariahism, but I would argue that all of it requires a bit of at least one of them. 

  2. ^

    For more about Braben’s approach to research management, see his book Scientific Freedom or this podcast I did with him.

  3. ^

    He didn’t actually use a quantitative ranking, but the Braben Venture Research Index in Braben’s less-known book, Pioneering Research: A Risk Worth Taking, gives a glimpse of his decision-making process.

  4. ^
  5. ^
  6. ^

    For more about Licklider’s approach, see the book The Dream Machine. Alan Kay also written a lot about it. 

  7. ^

    Arguably DARPA was a drastically different organization before and after 1972, but the core DNA was the same.

  8. ^

    Obviously not all grants are the same and there are many differences between FROs and startups. Institutions exist on many more axes and this is just a (albeit interesting) projection onto two of them.

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