Photo and blog by Kat Smith

Health inequalities researchers increasingly agree that we need to move beyond describing problems towards identifying solutions. But will better evidence about solutions be enough to create change? 

A thought-provoking new paper by Julia Berenson and colleagues asks why, after three decades of rapidly expanding research on the social determinants of health, progress in reducing health inequalities remains so limited. The authors argue that research needs to move beyond describing inequalities towards developing and implementing solutions, calling for greater methodological pluralism, interdisciplinarity and participation. 

There is a great deal here that I agree with. But I was also struck by how familiar the conversation felt. 

A few years ago, in a paper led by Michelle Kelly-Irving, colleagues and I argued that decades of health inequalities research had already taught us a great deal about what causes inequalities and that, in trying continually to refine this knowledge, we risked disappearing down methodological ‘rabbit holes’. More recently, in Getting Better: The Policy & Politics of Health Inequalities, Clare Bambra, Julia Lynch and I started from a similar frustration: most health inequalities research describes or analyses inequalities, so what might we learn instead from places and periods in which health inequalities actually fell? 

There is perhaps an irony in a field concerned about not being sufficiently joined-up repeatedly rediscovering similar arguments in different places. But it left me thinking we probably need to reflect more on why these arguments remain so necessary and what might help us move forward. With this in mind, here are my reflections: 

What would genuine methodological pluralism look like? 

There is considerable agreement that health inequalities research needs greater methodological pluralism. Berenson and colleagues call for moving beyond a strong focus on descriptive social epidemiology through greater use of policy and systems research, implementation science, political economy, modelling and participatory approaches. Our earlier ‘rabbit holes’ paper similarly argued that the complex causation underpinning health inequalities cannot be understood through increasingly narrow approaches to causal inference alone. Getting Better put some of this into practice, using comparative historical case studies to learn from periods in which health inequalities actually fell, even where the effects of individual policies could not be neatly isolated. 

My own thinking on this has also moved on. Since writing the ‘rabbit holes’ paper, I remain convinced of the value that approaches such as modelling can offer, particularly through working with researchers using models in policy-facing contexts. But I've also become more conscious of their limits. Methodological pluralism surely means not simply expanding our methodological toolkit, but being clear about the different questions different methods can answer – and the kinds of knowledge they inevitably leave out. 

Computational modelling, for example, can feel almost magical in its capacity to translate data about what happened in the past into projections of what might happen under alternative future policy scenarios. But models inevitably remain shaped by the data, knowledge and assumptions available to them. There is innovative work trying to push beyond these constraints. In our Enhancing Policy Modelling for Health network, for example, Ellen Stewart, Clemmie Hill O'Connor, Robin Purshouse and Shraddha Bhamare-Ghatkar have been exploring how young people's accounts of struggling to find meaningful work might inform models, rather than simply relying on the variables captured in existing datasets. An important question, though, is whether decision-makers will trust and use models that depart from more traditional approaches to what can be tested and validated. 

There is also a difference between calling for methodological pluralism and genuinely valuing different forms of knowledge. Despite widespread rhetorical support for mixed methods and participation, qualitative and experiential insights can still find themselves having to work rather harder to establish their legitimacy – challenged, for example, because they are not statistically ‘generalisable’. But applying criteria developed for one methodological tradition to another isn't methodological pluralism. Genuine pluralism requires us to take seriously what different forms of enquiry can tell us on their own terms. 

Effective interdisciplinarity requires humility and curiosity  

Greater interdisciplinarity is also part of the answer, but I think this requires some humility from health inequalities researchers about where relevant expertise sits and what we have to offer. Saying that people need better housing or better jobs is not the same as knowing how to create more equitable housing and labour markets. There are whole fields of research grappling with these questions, including the complicated political, economic and institutional reasons why apparently widely supported goals can be so difficult to achieve. 

So rather than only asking what other disciplines can bring to health inequalities research, perhaps we should be asking what we can learn from them – and what we can usefully offer in return. Evidence that poor housing damages health, for example, can strengthen the case for improving housing conditions. But people working in housing research and policy are already trying to improve housing and address homelessness. I am increasingly unsure that more evidence of the health consequences of poor housing is the evidence they have been waiting for. What health inequalities researchers may need much more of is their expertise: understanding why achieving better housing is so difficult, where the possibilities for change lie, and what kinds of evidence or collaboration might actually help. 

Genuinely interdisciplinary work, then, perhaps needs to start less from ‘how can other disciplines help us tackle health inequalities?’ and more from ‘what can we learn from each other, and what can we achieve together?’ 

From studying problems to co-designing solutions  

Both the new paper and our earlier ‘rabbit holes’ paper call for greater attention to the experiences and knowledge of communities most affected by health inequalities, and this is also an important theme in Getting Better. There seems to be growing agreement, then, that we need to get better at bringing lived and experiential knowledge into health inequalities research. 

But this also comes with responsibilities. As Ruth Patrick and Maddy Power have argued, there are important ethical questions about repeatedly asking people experiencing poverty and inequality to share difficult, sometimes traumatic, experiences when there is no guarantee that doing so will lead to change. Patrick and Power's focus on the ‘ethics of hope’ is particularly helpful: participation can create expectations that contributing your time and experiences might help make things better, while the consequences when change doesn't happen fall very differently on researchers and on people actually living with poverty and inequality. 

Perhaps one way forward is to shift more of our attention from involving communities in documenting problems towards co-designing potential solutions. But that requires more than researchers and people with lived experience working together. At a minimum, I think this means bringing four kinds of knowledge into conversation: researchers with relevant expertise (broadly conceived!); communities experiencing intersecting inequalities; frontline services and local decision-makers, who hold crucial implementation intelligence about how policies and services actually work; and national policymakers, who understand - and importantly have some power to change - the wider policy environment. Each holds different knowledge, and successful co-design requires all four to recognise the value of the others' contributions and to buy into the process. 

That feels some way from where we are now. Perhaps, then, one thing researchers who believe in these approaches need to do is make a stronger case for them – not simply advocating for more ‘public involvement’, but for processes that genuinely redistribute some of the power to define problems, develop potential solutions and shape policy. 

There are good reasons to invest our time here. Participation isn't simply a way of generating better knowledge or designing more implementable policies. One of the striking findings from Getting Better is that greater political incorporation and democratic participation recur in periods in which health inequalities fell: from civic activism and political enfranchisement around the Great Society reforms in the USA to participatory governance, stronger civil society and trade-union voice in Brazil. The book identifies several plausible pathways through which democracy might matter, including better policy responsiveness, greater social solidarity, and the psychosocial effects of hope and believing that change is possible.  This also connects strongly with Katie Hirono's work on democracy as a social determinant of health.  

So there are potentially two gains here: participation may help us develop more effective, implementable solutions, and meaningful democratic participation may also be part of what creates healthier and more equitable societies. 

Are we replacing one empirical hope with another? 

This brings me to perhaps my biggest concern. Health inequalities researchers have spent years worrying that ever more evidence about the problem isn't generating enough action. I wonder if we now risk replacing that hope with another: that if we produce better evidence about solutions, policymakers will act. 

Better data, models and evaluations can all help us understand what might work. But knowing more about potential solutions isn't the same as knowing how to make change happen. 

Policy change is political. The examples in Getting Better make this very clear. The kinds of reforms associated with substantial reductions in health inequalities didn't happen simply because the evidence for action became sufficiently compelling. They became possible within a particular political context, involving political leaders, civil-rights mobilisation and growing societal pressure for change. 

So perhaps health inequalities research needs to get more comfortable with questions that can feel distinctly uncomfortable: power, interests, public narratives, political strategy, coalition-building and advocacy. Evidence competes with other ways of framing both problems and solutions; powerful interests may resist change; and public narratives help determine what policymakers and publics believe is fair, necessary or even possible. 

This also raises awkward questions about our own role as researchers. Where does research end and advocacy begin? Should we be challenging damaging narratives, communicating evidence more strategically, building alliances or working alongside organisations seeking policy change? Different researchers will draw those boundaries differently, but I don't think we can simply avoid the questions. 

If we already know a great deal about the kinds of changes likely to reduce health inequalities, perhaps we need to spend less time asking, ‘what additional evidence do we need?’ and more time asking, ‘what would make action on what we already know possible?’ 

That means becoming much more serious about how change actually happens and about the role researchers might play in helping to make change possible.