The Opportunity Cost of Misdirected Talent: An ARPA Counterfactual

Speak to any UK researcher, and you'll be surprised about our strength of opinion on buckets. Since April, all research funding has been split between three main pots: curiosity-drive, strategic needs, and supporting innovative companies. Bucket 1 is responsive, distributed, investigator-led, designed to push research beyond the known. Bucket 2 is targeted, strategic, directed.

Responsive, curiosity-driven funding is effectively falling (historic 'block grants' have been wrapped into Bucket 1) while Bucket 2 increases; the government wants to see return on investment. While this is a UK-centric funding drive, it represents a wider capital allocation story.

What might the impact be of a more directed approach to innovation? Huge amounts have been written, but I am already seeing behavioural change in how scientists describe their impacts; far less 'foundational knowledge' and far more 'application-informed' research. On sift panels, I am being asked to assess what is most likely to succeed in this new world. And STFC-area early-career fellowship discovery-science applications are quietly becoming EPSRC-applicable instrumentation development; out is the awe, and in is the impact.

There's a fascinating parallel from the 1950's, in the establishment of two widely copied funding approaches, whose own fortunes have risen and fallen over the decades: The National Science Foundation (Bucket 1) and the Advanced Research Projects Agency (Bucket 2).

We can learn from the benefits - and risks - of directing research by studying the most copied funder structures in history.

Innovating in innovation: the ARPA model

People love the Advance Research Projects Agency (ARPA) model. From the business school researchers who try to distil the essence of innovation to translate - with mixed success - to industry, to the policy makers building replica agencies (ARPA-E, IARPA, or even ARIA) with different macro-goals.

At the centre are the PDs, who are borrowed - often from academia. These are the atomic unit of research focus, and the genius of the ARPA model is in the relentless focus on fixed-term secondments over institution building; the nexus of funding, responsibility, and empowerment lies in a single individual. It is widely admired and often copied.

But over it's lifetime, I'm not sure that the counterfactual has been robustly questioned: would innovators have produced more and better research outputs if ARPA had not existed? And what can this tell us about bucket of research funding?

The Gradient and the Pin

All universities have a research strategy. When I am on a hiring panel for new academics faculty, I am faced with a more prosaic choice: do we bet on the most promising person, or do we recruit to a more narrowly defined pre-defined growth area? There's never an easy answer - in essence, we are choosing between our own Bucket 1 and Bucket 2, with our expert panel having to agree on the Pareto front of curiosity and strategy. And our conversation always reaches 'but how will they fund their research?'

Ten years before ARPA, Vannevar Bush delivered his report to the president, claiming 'basic research is the pacemaker of technological progress'; this document set the founding model for the NSF. The Bush model implied that the frontier of knowledge has a gradient, and the people standing closest are the only ones positioned to know which direction is worth climbing. In Stokes' framing, this rewards Niels Bohr-type researchers: a quest for fundamental understanding, without a-priori consideration of application.

Traditional funding agencies use responsive funding to allow the community to hill-climb. ARPA flips this on its head - PDs put an (ambitious) pin in the map, and funding whoever can be persuaded to work towards this, regardless of whether this direction is most promising or whether the person funded was best placed to do the work. ARPA seeks Pasteur's quadrant researchers, who can deliver fundamentals and application.

The question is, does redirecting researchers cost you the destination, or does it cost the advantage of the researcher already being at the frontier?

A research redirected to Pasteur's quadrant does not automatically become more useful or productive; they may in fact lose the advantage of domain knowledge that made the valuable. The enthusiasm for Pasteur's quadrant risks treating all redirect as productive, where it can just as easily be resource misallocation.

This isn't an unambiguous defence of Bush's NSF; delegating responsibility to peer review can just as easily turn into 'giving money to smart people', lacking procedural accountability in a different way.

The Value in Not Knowing You've Won

The scientists that advised ARPA were the JASONs. This group of - initially all male - academics over-indexed on theoretical and nuclear physics, and went on to include 11 Nobel Prize winners. This group would have been successful with NSF funding, and did not just include those involved in defence research; their inclusion was a clear redirection of some of the most valuable research resource in the USA.

While we will never know the totality of their output, we do know that defence spending typically provides a 1-2x ROI compared with 8x for public R&D. But what about the moonshot successes unique to the ARPA model?

The most common civilian successes cited for ARPA - the internet or seismology underpinning the theory of tectonic plates - survived because the flat autonomous structure of ARPA didn't know what projects to protect or to kill. In essence, they were civilization-scale wins despite having emerged from human-computer symbiosis (not nuclear command-and-control) and nuclear anti-proliferation; ARPA's structure allowed them to succeed.

However, other well known projects such as the Grand Challenge (autonomous vehicles) and the Red Balloon Challenge (social engineering) were PR exercises dressed up as research funding. The former cost far more to run than it awarded to the winners, and the latter used capability that had long been available - neither meaningfully contributed to the development of the fundamental capabilities in the fields.

The Principal Problem

What links these behaviours? The most intriguing aspect of ARPA is the principal-agent question. Resources flowed via the Pentagon (the principal), who expected defence innovation while (mostly) accepting ARPA's unique role in high-risk and early stage work. ARPA (the agent) provided the structure for delivery of innovation. But nothing comes for free - all principals expect return on investment, and in domains where work is hard to assess but results are easy to measure, the agent is incentivised to reduce risk and deliver results.

For defence-aligned research, the fundamental 'Pentagonian Bargain' that the organisation can maintain autonomy and secure resources holds when stakes are low, and breaks under pressure. This is particularly clear from the TIA programme, with a deep civil liberties failure a 'dishonest misuse of DARPA'.

These are not criticisms of the ARPA model per se; defence R&D is not inherently a problem, and the programme-officer model can survive and translate to a positive-sum principal, such as at the Gates Foundation. But the principal's own incentives dominate the agent's autonomy in practice - and it is precisely this that can lead to a hidden drive towards misalignment.

And while a clearer public-service remit for research has been used in derivatives of the ARPA structure, most notably in ARIA, this has not provided immunity against criticism of their investment decisions. Accusations of poor return to stakeholder will persist, precisely because the process of high-risk research is impossible to evaluate, but the cost is all too tangible.

Pay for What, Exactly?

Research needs resources. High-risk, frontier research needs a lot of resources - and implicitly require stakeholders to agree on the risk appetite. If the agent's risk appetite is mismatched with the principal's, misdirection of resource is a concern.

On the face of it, this presents a conflict: bucket 1 research is high risk for the principal (will it pay off for the taxpayer?) while bucket 2 is high risk for the agent (will this reward for the researcher?).

Hanson proposed an alternative framework; paying for results, not process. When the outcome is evaluable, the principal is low-risk appetite and the agent is high-risk appetite, we can reward outcomes rather than effort. This is the university model, where promotions follow observable successes. This is the correct contract, and realigns mixed risk appetites; reward follows measurable (or proxy) success because process cannot be measured, and I've written about how we might approach this in practise.

ARPA breaks this model as a funder, because both the principal and the agent are risk-seeking. The mid-term reviews are neither pay-for-results or pay-for process. And while the funder and the research are aligned, the resources are provided by a low-risk body: ultimately, government and taxpayers. ARPA could not be assessed on process, and when assessed on outcomes may not be value for money.

Their durability as an organization became tethered to political maneuvers, and their remit as a unique capability to deliver for a defined and cost-insensitive market - the DoD; This backstop does not exist for public-service funders.

The Counterfactual We Can't Run

The opportunity cost of redirected science - be it ARPA or Bucket 2 - is invisible, because the paths not taken cannot be observed. Despite over 60 years of operation, we do not have a mechanism to approximate this cost.

What is clearer is that the return on awe - the Bucket 1/NSF model - and return on investment lie on different axes. The ROI-based critique of ARPA misses that their research often produced neither; would researchers have otherwise studied the psychic abilities of a magician with taxpayer's funding?

We now have enough ARPA derivatives with different principals and risk appetite - ARPA-E, ARPA-H, ARIA, Gates-style - to understand which aspects of this experiment in innovation are valuable. This isn't a novel provocation - the IFP's Caleb Watney has been pushing this question for years even without a shared counterfactual framework.

And the Buckets? Writing a recent grant proposal I found myself having to frame a study as foundational, or to define an application focus. This felt uncomfortable, because I did not know whether I was protecting the taxpayer or replaying the 'Grand Challenge', prioritising legible impact today over the understanding that will matter in twenty years.

I do not have a mechanism to measure my own opportunity cost of short-term impact focus over long-term curiosity focus, but neither does my institution or UKRI. And with sixty years of the most copied funding models in history, nobody has built a counterfactual tracker.

I do not believe that bucket 2 is wrong, or that ARPA was a mistake. But any funder - government or neo-lab - that redirects talent without attempting to price what this gives up is running an uncontrolled experiment and calling it a strategy.

Bounding What You Can't Predict

It is tempting to try and build a system that predicts optimal pin placement...but that's wrong for AI-for-materials and a category error applied to one-off research. Instead, we must shift our mindset: there is no value in attempting to optimise the research direction of exceptional talent, but there is systemic value in shifting the median. My own research is built on the premise that you must design recipes to improve distributions, not the hero device - a single champion result is statistically indistinguishable from a lucky draw.

The same logic applies to a portfolio of ARPA-style bets: the JASONs are the hero devices, for whom (mis-)direction is always a cost. Instead, we must avoid making the worst allocation of talent - the Red Balloons with empty impact, the Bohr-to-Pasteur costs where researchers are ill-equipped to make this transition, the TIA-type principal capture.

For UKRI or for a neo-lab, the goal is not to gamble well but to bound the tail risk of misdirection — and it is exactly this discipline, not a better prediction of the pin, that unlocks the upside: capital and talent freed from funding empty Red Balloons is capital and talent available for the next unpredictable Bohr. The right question was never 'who is the next Pasteur', but 'how do we stop funding the next Red Balloon.' Shifting the median beats chasing the outlier, because the outlier was never ours to find.