If we were to take the UK’s Advanced Research and Invention Agency (ARIA) seriously as a project to develop new kinds of R&D, how likely are we to view it positively in a few year’s time?
The stated inspiration for ARIA is obviously the American DARPA, an integral part of the US weapons system. DARPA suggests quite narrow readings of the history of American innovation driven by relentless, undemocratic and autarkic ideas of technology that draw heavily on Moore’s Law (and which have now been applied to much of the rest of science policy). Whether this agenda is compatible with civilian challenges across the board and in a smaller and less competent national scientific context like the UK is open to question.
Over the past few months, ARIA has published around a dozen of what it calls “programme theses” laying out its investment plans (about 50m GBP per thesis). Studying the fine details of these helps us answer that question.
My diagnosis is that the agency is struggling to detect promising new lines of research, with enthusiasm spilling over into wishful thinking.
The initial hurdle we face is in working out what ARIA is supposed to be doing and therefore whether it is likely to achieve it. The underlying legal text, the Advanced Research and Invention Agency Act 2022, specifies that ARIA must contribute to “economic growth, or an economic benefit”, promote “scientific innovation and invention” and improve “the quality of life”.
Citing different wording on its website, accessed this February, ARIA “empowers scientists and engineers, from our Programme Directors to the teams we fund, with the resources and freedom to pursue breakthroughs at the edge of the possible. Many will fail to meet their target, but their efforts will inspire the next generation. Those that do succeed will generate massive social and economic returns.”
The website also states that ARIA is “built to unlock scientific and technological breakthroughs that benefit everyone”.
It seems to me therefore we might summarise the strategic goal as producing “economic benefit” and improving “the quality of life” based on promoting “scientific innovation and invention”.
This is a low bar and could be achieved by anyone, simply by donating a few coins to a medical research charity. The lack of bureaucratic ambition is, as it were, incredible. But we also have to consider that the agency could produce negative effects that, unlike the hypothetical donation to medical research, undermine its own goals.
The legislation notes the possibility of failure by inciting the agency to undertake the “development and exploitation of scientific knowledge that carries a high risk of failure”. To put it in simple language, it seems that this invitation of “failure” runs the risk of becoming an invitation to just that.
First, I want to sketch my own mental model of how public investments in civil R&D would, logically, be decided, and then compare this to ARIA.
The core negotiation in R&D policy is typically between political goals, the difficulty of shaping nature to human will, and limited capacity in science. For example, the UK’s now defunct but once legally-independent research funding councils addressed national capabilities by knowing the “landscape” through regular consultation with the expert community, tracking promising lines of investigation through their network of scientific contacts, and varying degrees of direction from officials and private firms, around which grant programs would be designed.
In my view, therefore, the “standard” approach would be to weave together existing resources: scientific, human, financial and political. The approach ARIA has chosen is different, as the “programme theses” have started to illustrate. They are based around the idea that R&D can be conjured out of a hat.
Fantasy football
To my mind, the contrast can be seen vividly through the choice of citations in the programme theses. Logically, a viable proposal ought to use its references to give an idea of exactly who the program managers intend to fund. This means they would need to cite promising lines of primary investigation led by individuals based in the UK, or who the agency believed it could recruit to UK projects. To the contrary, ARIA seems often to cite review and op-ed articles – not peer-reviewed primary research – and the citations are to authors without connection to the UK such as in China and the USA.
It ought to be taken as a general rule that attempts to directly compete on technical grounds with established American and Chinese activities is a dead end. This takes a swathe of topics off the table such as AI, microchips and robots and to my mind therefore renders invalid many of the above programme theses (marked with †). At least, it sets an extraordinarily high bar to establish and promote niche expertise and the theses certainly have not clarified it.
In the field of climate change (marked with ‡), ARIA has detected that the UK has valid national capacity in climate modeling, but that was already widely known. It is also public service science. This should be encouraged and promoted but it is not the logical primary role for ARIA. In my view, ARIA’s role would be better packaged as part of a climate change response platform. This would need to be driven through international collaboration such as with the EU and Asian countries in conjunction with UKRI and relevant ministries, local and devolved governments. Whether or not UK (and overseas officials) have the interest in making this happen is unknown to me. If they lack that interest, it would be a hard road.
The thesis “Enduring Atmospheric Platforms” seems to be a topic for military research and might also, logically, need to acknowledge the aerospace community such as through the existing roadmapping activities of the Aerospace Technology Institute, the former UK Space Agency, Catapults. It seems like this is quite a bureaucratically turbulent area and perhaps the immediate problems are finding a way to weave together knowledge and expertise rather than founding another technology programme.
Chance and necessity
That leaves the five biology theses marked in the table with * that I will now consider in greater detail. The first thing to say in general is that biotechnology has existed as a significant industry for more than 40 years and therefore most, if not all, ideas have probably been considered before, nor is ARIA the only foresight organization in the field.
Let us take as emblematic the thesis “Sustained viral resilience by strengthening innate immunity”. It is based on the premise that “vaccines against infectious disease were the first medical fruits of leveraging the adaptive immune system as a tool” and now the time is ripe to explore how to stimulate the innate immune system.
The problem is that the premise is untrue. Historically, vaccines have been developed by trial and error and target both the “innate” and “adaptive” immune systems. Indeed, it is not really known exactly how vaccines work, nor, to be honest, how the immune system works. The rigid dichotomy that ARIA uses as its premise is, therefore, problematic and itself deserving of proof. The science of adjuvants, which are typically understood as stimulants of “innate” immunity might be relevant, but is not raised. It would be better if the proposed work engaged with discussions around the future of vaccinology which talk about such topics as mucosal immunity and vaccine acceptance.
Although the UK covid vaccine turned out not to be the market leader, it was a good effort, yet for reasons unknown the British have not really digested the implications of their success. One of which was nurturing a tradition of scientific expertise through many decades of low-key, consistent investment in relevant biological research. It is as yet unknown if the covid vaccine will come to be seen as the last hurrah of the UK in this field.
In the future, there is no doubt governments around the world ought to be spending more on research on infectious disease countermeasures. But there are already frameworks in play for this, such as the “100 Days Mission” and the WHO’s “Pathogen X” research roadmap (under development), where ARIA could in theory make contributions.
Another ARIA thesis, “Synthetic plants for a sustainable future”, aims to “build, deliver and maintain synthetic chromosomes and chloroplasts that are viable in potatoes and in an unspecified monocotyledon (such as grains). Regulatory objections aside, genetic engineering of crop plants has proved extraordinarily difficult from a technical perspective, despite decades of effort. Only a few dozen crops are known to have been engineered; fewer still have been widely planted, namely, Bt and glyphosate resistant varieties. ARIA’s thesis therefore sets a very high technical bar.
This is an arcane field dependent ultimately on intricate experiments that only a few labs are able to conceptualize, let alone successfully execute. It is currently impossible to deliver a plant chromosome into a plant cell. The largest cassettes claimed to have been delivered have been about 200 bases in size, whereas a plant chromosome is ten to hundreds of megabases, i.e., “considerably out of range” of existing technology, citing a knowledgeable source.
Another story might be told for the chloroplasts. However, for unknown reasons, ARIA does not reference the most pertinent experiments, notably, the “chloroplast-mimicking droplets” by Miller et al., Max Planck/CNRS, published in 2020. In 2024, Aoki, et al., University of Tokyo, reported having introduced an isolated algal chloroplast into a mammalian cell while preserving photosynthetic activity for two days. These experiments have, however, been done in tiny volumes of liquid that are not currently known to be scalable.
In my view, the proposal needs a significant rethink and in light of the reality of UK expertise in plant biology, which has for the most part been run down with closure of applied R&D over the last few decades. The broader question of whether biotechnology is the key to “a sustainable future”, even if it could be made to work, is rather important.
Quick comment on the other biology theses:
- “Massively Scalable Neurotechnologies” seeks devices that “sense, interpret and modulate pathological neural activity” without invasive surgery. It implies an enormous weaving together of diverse research programs across vast areas of human knowledge. It cannot be serious without asking first what, for example, the NIH foresights on neurological disorders. But, even this kind of basic background scoping work has not been done.
- “Precision Mitochondria” concerns genetic engineering of mitochondria. It is a specific topic and techniques are reported to have improved over the past decade. However, in such a highly technical area like this, which I believe cannot just be undertaken by anyone, and is therefore largely the province of a very small number of specialist labs, we must ask what national capacity looks like. Here the programme thesis is lacking. This is really a question of working explicitly with UKRI, such as the MRC, to understand what the UK capacity looks like, what is already being done to support it and how ARIA could contribute within a shared strategic framework.
- “Universal fabricators”. Talk of “a new protein age” is marketing. ARIA needs to identify the primary scientific research underpinning any proposals and describe how lines of investigation could be realistically taken forward in the context of UK scientific capacity.
Conclusion
In the twentieth century, British science and technology policies often focused on creating large, intricate objects such as the Concorde supersonic airliner and the Advanced Gas Cooled (AGR) nuclear reactor. However, these came to be seen by some as white elephants; others later declared that lessons had been learned and, therefore, the same mistakes would not be made again.
On the contrary, you could argue that the same mistakes were made again (and again), it was just that the white elephants changed their political appearance. Instead of being objects, they became concepts, such as biotechnology, nanotechnology, AI and quantum.
It is indeed possible that more public funds were spent overall on these concepts than were ever spent on Concorde and the AGR, but with what results, perhaps much less than hoped.
ARIA was claimed as an innovative addition to the British scene. But there is no such thing as a clean slate. Indeed, UK S&T policy was always determined in a rather undemocratic and autarkic way and, as such, models akin to DARPA are familiar to the British ethos and therefore likely to succumb to the same general problems. This means objective thinking is going to be as hard as it often was in the past.
However, stepping outside the conventional moralizing about S&T policy, I believe the following specific points are worth making:
- America’s DARPA and ARPA-E focused on narrow fields of application, namely weapons and energy, encouraging deep expertise, and were tied to the relevant government departments, respectively, defence and energy. It is impossible to build the needed expertise across a vast range of topics as ARIA has attempted.
- Each project is different and calls for a bespoke approach. Some problems do not yield to brute force. Yet the relentless ARIA model of standalone technology programmes does not evoke much flexibility.
- ARIA must be able to accurately detect UK expertise and promising lines of investigation. It does not seem currently inclined to do so.
- The agency must get better at understanding existing foresight processes and frameworks around the world and position itself within them.
In a utopian world, it would be an idea to cancel all the unstarred projects noted above, then take a deeper look at the remainder with a view to taking forward at most 2-3 with revised strategies and raised budgets, that is, if they still passed muster. Otherwise, back to the drawing board. (I would say, if you have a good plan that you release in public, it is an idea to have a big budget to discourage others from thinking they can outbid you with knock-offs.)
Unfortunately, I am not aware of a mechanism within the bureaucracy to respond to the challenges raised here and consider strategic corrections. ARIA’s legislative invitation to failure and its seeming rigidity in terms of approach risks a tendency to stubbornly plow on. Often, the science policy issue is not aversion to failure, as such, but unwillingness to change course. This leads to a confusion between political efficacy and actual results, with the former typically winning out.
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