An ARIA for social issues?

The case for exploratory social science

Should the social sciences primarily focus on analysing the world - or should they try to help fix its problems?

To crystallise the question in this piece I ask: why is there no ‘ARIA for social issues’ (or an equivalent in other countries)?

ARIA – the Advanced Research and Invention Agency - is the relatively new institution created in the UK to back breakthrough innovations in science. The government recently awarded it an enhanced budget of £1bn. It already finances teams working on topics like bio-energetic engineering and programmable plants. I like both their approach and their projects.

But it’s remarkable that there is nothing comparable for social science, and no lobbying from the various bodies responsible for the social sciences for anything similar. Many of the UK’s most pressing needs are every bit as much about social and economic challenges as they are about scientific ones. It’s possible there is a good argument for spending £1bn on breakthrough science and £0 on breakthrough social science. And it’s possible that someone could mount the argument that all of Britain’s problems, and the public’s perception that the nation is ‘broken’, result from a lack of science rather than a lack of social and economic solutions. But I’ve never heard it (more on ARIA later).

The quadrant four problem

This failure, and this imbalance, reflects a much deeper problem. A simple way of understanding it is through a framework for thinking about the current activities of social science. The four quadrants below categorise research by whether it’s concerned with diagnosis and analysis of the present and past, or prescription, designing options for the future. Another axis considers how much research is incremental diagnosis and prescription, perhaps looking two to three years into the future, and how much is radical diagnosis and prescription looking decades into the future.

This framing gives you a matrix with four quadrants: incremental diagnosis, radical diagnosis, incremental prescription, and radical prescription.

I argue that social science today has become overwhelmingly oriented towards quadrant 1, with small amounts of activity in quadrants 2 and 3, and remarkably little in quadrant 4, which is where you would find radical prescriptions for 20, 60, or 100 years into the future.

This is a very strange development and makes the social sciences strikingly different from the natural sciences, which invest heavily in radical prescription. Funders for artificial intelligence, new materials and genomics, spend generously on imaginative speculation and risky ideas. So does the medical world, which is reasonably balanced between the four quadrants, with many researchers and doctors working on current diagnosis and prescription, but many others looking far out into the future, working on equivalents of innovations like mRNA, which had such an impact during the COVID pandemic, or the next generation equivalents of Ozempic or surgical treatments of all kinds.

There are many reasons why social science has given up on this space. It reflects a broader shift away from interest in progress and the future towards anxiety, worry and risk. Some suggest it’s an unfortunate side-effect of the often-healthy focus on data and evidence since these are by definition concerned with the past and not the future, but have crowded out future thinking (whereas in fields like medicine they haven’t). Another factor is politics. In the US the main justification philanthropists and big foundations make for not funding any exploratory social science is fear of political controversy or even retribution.

But some of the fault may lie with leaders in the social sciences themselves. As far as I am aware none make the case to funders or government that exploration matters, and that we have a shortage of good options for the future.

And too few of the best social scientists bridge the four quadrants in their own work. In this respect they are different from many of their predecessors. Many of the greatest social scientists managed to fuse diagnosis and prescription, incremental and radical ideas. This was true of figures in the distant past as varied as Jeremy Bentham, John Maynard Keynes and Florence Nightingale and more recent ones like Elinor Ostrom, Rhona Rapoport and Amartya Sen.

However, when I talk to younger social scientists, most say that they have to concentrate on quadrant 1: it's essentially career-threatening to work on designing speculative options for topics like the future of democracy or welfare. Far better to diagnose the ills of the present than to work on possible solutions.

If you doubt what I'm saying, try searching in social science academic journals on any topic to find the ratio of analysis of the last 50 years (back to 1975) compared to options for the next 50 years (up to 2075). Is the ratio 1 to 1, 5 to 1, or 50 to 1? Most who've attempted this, and it's quite a difficult task to do precisely, suggest the ratios are something like 100 to 1. There is a reasonable amount of quadrant 3 work, which is very incremental policy options and guidance to the professions, including nearly all of what's called policy engagement in academia. There's still a fair amount in quadrant 2 of critique and commentary, in the traditions of academic Marxism and post-Marxism which remain strong in some universities (commenting on meta-crises and poly-crises, neoliberalism and the Anthropocene), and there is also quite a lot from the far right that is essentially critique and commentary.

But as for quadrant 4: very, very little. There is occasionally an article exploring forecasts and scenarios or saying that we need a new plan, a new Beveridge or a response to some big challenge: but usually they say very little about it might actually contain. There are a few exceptions, like Gabriel Zucman who is working vigorously on tax reform. But they are very much the exceptions.

A good illustration is the field of institutional design (which is a main focus of my work with The Institutional Architecture Lab). Last year's Nobel Prize for Economics went to Daron Acemoglu and his colleagues for brilliant work showing why institutions were the fundamental cause of long-run growth and societal prosperity in the 20^th century. Their work is impressive in detail. Yet they have done no comparable work on the obvious implication of their research, which is that institutional design now and for the future could be just as important in determining which nations prosper in the 21st century. They simply don’t see this as their job and as far as we can see there is no social science funding for institutional design as opposed to analysis of institutions in the past.

This seems to me a remarkable shift and a big problem in a society that may have lost confidence that it knows its pathways to the future.

I’m interested in what should be the methods, the means and the structures that could help us flesh out quadrant 4 and what I call a more exploratory social science (I’ve written a book on this which Oxford University Press will publish in 2026 ).

Such exploratory social science would build on existing methods in design and mechanism design, modelling, systems and complexity and many other fields, to flesh out specific ideas and options relevant to domains like the economy, politics, health, or environment, which could then be adapted through experiments and practice. It could build on initiatives to better integrate social science and social change (like Cardiff’s social science park). It would need very different methods to ARIA, not least with much more engagement with civil society and communities at multiple stages.

And it could be helped by "what if" exercises. What if, for example, democracy was redesigned for the 21st century? We have plenty of potential building blocks from quadratic voting to sortition, citizens assemblies and deliberative juries to multi-level participatory budgeting, AI tools like Poli.s and new laws to strengthen truth in political communications. How might those be pulled together into a roadmap for reimagining democracy?

Or, what if we found more creative ways to use time, given that life expectancy is roughly double and the working week is roughly half what it was two centuries ago. Populations are both older than ever before but also have more years left to live than ever before. Again, there are many ideas to build on, from time banks and city time strategies to four-day weeks and lifelong learning. How might those be pulled together into a coherent program?

Some of the barriers to this kind of work mirror those in other sciences. Many point to the excessive power of disciplines policing their boundaries – and so blocking off the transdisciplinary work needed for this kind of work. Many blame peer review: while good analysis quite easily passes peer review, anything involving design or creativity seems to almost always be killed by peer review processes (or to put it another way, if you want innovation, get innovators to do the peer review).

In science, the widespread recognition of these barriers has encouraged plenty of innovation, particularly from individual philanthropists in the US - with more open ended funding of teams, individuals, programmes, and new models like Focused Research Organisations. But there is no comparable funding for good exploratory social science, and therefore no incentives to specialise in it. For example, the Economic and Social Research Council (ESRC), led by the very able Stian Westlake, invests heavily in trying to understand the problems of UK productivity but feels it does not have a license or authority to fund the design of radical (quadrant 4) potential solutions in this or other fields (strangely, the Arts and Humanities Research Council (AHRC) does rather more future-oriented work with its very limited resources).

Some philanthropic foundations deserve credit for doing more exploratory work, including The Resolution Foundation, the Joseph Rowntree Foundation and Nuffield. But even their time horizons tend to be at most 10-20 years, even though life expectancy for children born this year is over 80, with many likely to live beyond 100.

There is some interesting work done on futures, but usually by people without much disciplinary knowledge, and usually outside universities, whereas the people with deep disciplinary knowledge feel they are unable to work on design options for the future (and because much futures work is flaky and vague, and not much interested in facts or evidence, it tends to de-legitimise activity in this space). In my book I will set out many potential solutions, including better ways of organising exploratory social science in disciplines, in universities and in hybrid institutions, and the kinds of team that do this work best. I also look at the role to be played by AI. One of many symptoms of the problem described in this piece is that very large sums of money are being spent now on using AI for evidence synthesis (including substantial grants from the ESRC and Wellcome adding up to well over £50m), but apparently none on using AI to help with innovation and design, or use of personas to help shape options, which are every bit as important for policy design as evidence synthesis.

This points to one more immediate solution: money. As indicated earlier, over the last few years, the UK created a new institution, ARIA (the Advanced Research and Invention Agency), partly modelled on DARPA in the US and more recent models like SPRIN-D in Germany. They have a budget now of about £1bn dedicated to backing teams doing breakthrough research in important and fascinating fields such as neural interfaces and robots. They allow their cross-disciplinary teams to speculate, think, and imagine, and then they provide additional support to help those teams put their ideas into effect, whether as commercial products and companies or as items which governments could procure.

I'm in favour of what ARIA is doing and how it is working, and I think it's entirely reasonable for the UK to spend a billion pounds on potentially transformative ideas. But I think it's impossible to justify that so much money should go on science and technology breakthroughs and nothing to equivalents in the social field.

That there are no comparable teams working on how care for the elderly might be organized in 2040, or parliamentary democracy, or services for people with disabilities, or childcare, or the everyday life of neighborhoods is extraordinary and indefensible (every now and then I search to see if there are any teams doing serious work on these issues: they may be hiding but I don’t find them. On care for example there are fantastic researchers studying the present problems or doing comparative analysis, but hardly any doing long-term design).

I've not heard anyone give any justification for this remarkable imbalance, let alone a good one. One insider told me that the issue had never arisen, and literally hadn’t occurred to the people making the key decisions.

If there was to be a serious debate about the option of a social ARIA, one anxiety is that any proposals are bound to be political, either explicitly or implicitly. That’s true. But the task for funders is to ensure a reasonable ideological spread, not to avoid design altogether, and of course many of the projects ARIA is doing are highly political in their implications (geo-engineering is just one example).

Surely it must be incumbent on the peak bodies like the Academy of Social Sciences, the ESRC and the British Academy, to make the case: if not for a billion pounds for exploratory social science, then at least for something. The Academy is chaired by Will Hutton who has a weekly outlet in the Observer and could easily make the case. So could university Vice-Chancellors, none of whom (I think) has ever addressed this issue. And so could the ESRC and UKRI in their very regular interactions with government. You might expect a Labour government to have at least some interest in social solutions – but as far as I know DSIT has never offered an opinion on any of these topics.

Perhaps a social version of ARIA could start with much smaller sums - £10 or £20 million, but with the same approach of backing teams to work on breakthrough radical innovations linked to the most pressing challenges facing the UK. As with ARIA these teams should combine university researchers from different disciplines with non-university innovators; they should be given space to push the boundaries of imagination; and they shouldn’t be overly constrained by academic peer review and disciplinary policing. Serious attention should be paid to methods - learning from new approaches to experiments, pilots, uses of AI and models in science like the FROs (Focused Research Organisations) or the Tech Labs now being funded by the US government ($30-50m for each team) - so as to avoid repeating the problems of past interdisciplinary projects which rarely moved beyond analysis to synthesis and prescription.

If Britain was absolutely confident and happy with its social arrangements and institutions this argument might have less weight. But we hear again and again that the public thinks it’s broken. Some want to burn down our institutions and start again. Is it really wise to have thousands of social scientists analyse the brokenness and to have so few working on how to fix the problems? Is it really wise to spend so much on scientific ideas and so little on social ones? I don’t think so.