Find inspiration and discover a research topic that makes a difference.

How to choose a research topic

Below are research directions that we think have high potential to improve the world by helping to solve pressing global problems that would particularly benefit from further research.

Several factors we suggest you consider when choosing a topic are:

If you're studying for an undergraduate or master's degree we often recommend focusing on developing your skills and knowledge in an area in order to contribute to solving a pressing problem later in your career.

If you're a PhD student you may be more able to contribute to solving a problem through your research already. You may also need to give consideration to building your reputation in academia and to whether your topic will 'lock you in' to an area long-term. The more likely this is, the more important it is that you choose an impactful topic which is a good fit for you! 

Check out our key ideas for more detail on how to choose a research topic. If you find a topic that you're interested in pursuing further, get in touch — we can help you make progress.

Explore and get interested

Check out all our recommended research directions here or click the disciplines below to see our profiles for your field of study.

There are several research directions we think might be especially high impact in making the world a better place. If you get interested in any of these topics, we can connect you with researchers working in these fields or provide other types of support (scroll to the bottom for more info). If you would appreciate more tailored advice, you can try our thesis topic coaching. Our list of prioritised research directions is not exhaustive, so there may well be some other high impact research directions that we have not yet covered. However, we aim to select impactful topics, so that chances of any of the topics we covered being highly impactful are higher than chances of average/randomly selected topic that we have not covered. If you know about research directions that could be similarly impactful to those we have covered, please, let us know.

Global priorities research

#discounting #growth theory #time-series econometrics #decision theory #mechanism design #value of information #behavioral economics #social choice theory

Why is this important?

What are the problems we should focus on to improve the world the most? How should we allocate our resources to do the most good? Despite being obviously important, these questions are surprisingly neglected. More insight into these questions could have a large influence on how successful humanity is in improving the world. Read more here and see the update here, or watch Will MacAskill's introduction to the goals and research of the Global Priorities Institute below.

How to tackle this

There are a number of themes in the Global Priorities Institute’s research agenda. Some examples:


“A catastrophic risk can be called ‘existential’ to the extent that it threatens a large, permanent negative shock to the subsequent growth path. An even more precise characterisation of this property may be valuable. How can we best model the magnitude of the permanent costs associated with a given risk? (Ord forthcoming)

...Much government policy, economic research, and philanthropic activity is intended ultimately to increase the general rate of economic growth. Economic growth could be extremely beneficial, from a long-term perspective, as it promises to improve the entire course of the future. However technology-driven growth may raise existential risks, due for example to nuclear accidents, engineered pandemics or artificial superintelligence (INFORMAL: Yudkowsky 2013), and growth in general may have other negative effects (for instance, risks to human life (Jones 2016), climate change (IPCC 2014), or meat consumption (INFORMAL: Bogosian 2015)). How radically do these drawbacks render growth an imperfect proxy for expected long-term wellbeing? Is the correlation between consumption growth and long-term wellbeing even positive, given the current drivers of growth, from a geographical, sectoral and technological perspective? (Friedman 2006; Cowen 2007; Tomasik 2013; Cowen 2018) (INFORMAL: Beckstead 2014) ”


“How should we adapt key economic models to account for altruistic individuals with other-regarding preferences (Bergstrom 2002, Sobel 2005)? Under what assumptions do key results, such as the Fundamental Theorems of Welfare Economics, still hold (Schall 1972; Pollack 1976; Rotemberg 2003)? In cases that they do not, can analogous results be derived?”

See also the research directions suggested by the Forethought Foundation.

Who are some of the people already working on this?

Economists doing relevant work: Chad Jones, Philip Trammell, Tyler Cowen, and Kevin Kuruc; to see an example of explicitly GPR-motivated economics paper read Leopold Aschenbrenner's "Existential Risk and Growth"; and there is also a number of other academic sources and pointers in the Global Priorities Institute’s research agenda. You could also look at the work of the Center for Reducing Suffering.

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Governance of artificial intelligence

#future of work #growth models #game theory #political economy

Why is this important?

Developments in artificial intelligence algorithms will likely have a significant impact on many aspects of our societies and lives. Research into how we should govern the development and deployment of AI will help us capture the potential benefits and mitigate the risks stemming from abrupt changes. To learn more, you can read this guide, watch this talk, and listen to this, this and this podcast.

In the video below Professor Allan Dafoe discusses the impact transformative AI will have on international politics and the urgent need for research on AI grand strategy. Read the AI Index 2021 Annual Report for an overview of recent data and insights about AI.

How to tackle this

A set of open questions and introduction to the field could be found in The Economics of Artificial Intelligence: An Agenda book.

There are also a lot of questions you can draw from this research agenda, for example, what will the impact of exacerbated inequality and job displacement on trends such as liberalism, democracy, and globalisation be; who should be leading on AI governance; how substantial of an advantage does China have, as compared with other advanced developed (mostly liberal democratic) countries, in its ability to channel its large economy, collect and share citizen data, and exclude competitors; to what extent are countries (e.g. Canada) able to internalise the returns on their AI investments, or does talent inevitably gravitate towards and benefit the existing leaders in AI (e.g. Silicon Valley); etc...

Yet another set of suggestions can be found in this post. Examples include “How plausible are safety concerns about economic dominance by influence-seeking agents, as well as structural loss of control scenarios? Can these be reformulated in terms of standard economic ideas, such as principal-agent problems and the effects of automation?; Which tasks will there be most economic pressure to automate, and how much money might realistically be involved? What are the biggest social or legal barriers to automation?” etc…

Some ideas for potential research projects are also here and here.

You can also see this guide featuring some additional questions and check some of our finished theses on the topic. You can sign up for The European AI Newsletter focused on AI governance by Charlotte Stix. Finally, this list from the Stanford Existential Risks Conference includes further resources for getting oriented in this area.

Who are some of the people already working on this?

Governance of AI team at the Future of Humanity Institute; Center for Security and Emerging Technology; Center on Long-term Risk; AI Impacts; GCRI; The Centre for Long-term Resilience; Centre for the Study of Existential Risk; AI Objectives Institute; Aghion; Jones & Jones; William Nordhaus; Korinek & Stiglitz; Prof Allan Dafoe

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Progress Studies

Why is this important?

Advances in science, technology, economic organisation, institutions, and culture have caused immense improvements in the standard of living over the past several hundred years. Increasing the rate of progress in these areas by even a small amount could lead to very large gains in the long-run (for example, increasing output by 1 percent per year would translate into 35 percent output in 30 years). Therefore research focused on identifying interventions and policies that would speed up the rate of progress could be highly impactful. Tyler Cowen and Patrick Collison proposed progress studies as a single discipline. You can learn more in this article or this podcast, or watch the video below for an introduction to the field.

The differential progress framework is a potential counterargument to the ideas that speeding up progress is beneficial. Harmful technologies might be developed before we know how to control or prevent their adverse effects (e.g., unaligned artificial intelligence). According to this argument, it is important to influence the order in which different technologies are developed rather than the overall rate of progress.

How to tackle this

One potentially promising avenue is to study how to organise institutions of science to increase their productivity. A new discipline named Science of Science sets out to do this in a quantitative, interdisciplinary manner. Some further related ideas can also be found in this series of posts at Nintil. Some people also argue for more structural diversification of scientific institutions and are putting together proposals of how new types of research organisations could be organised (for example, see Samuel Arbesman’s list and José Luis Ricón’s list).

Inefficient practices and technology often persist despite the availability of better alternatives. For example, Bloom et al. (2013) show that providing consulting on management practices to randomly chosen Indian textile firms increased their productivity by 17%. Further research could address why firms do not adopt more productive practices (although this area might be less neglected, see e.g., Comin and Mestieri 2014 for a review of literature on technology diffusion).

Finally, we need to better understand how (and to what extend) we can shape the direction of technological progress to avoid development of harmful technologies. Research in this area could build on the literature on directed technical change, which has been studied both theoretically (Acemoglu 2002, Acemoglu et al. 2012, Popp et al. 2010) and empirically (Popp 2002, Hanlon 2015, Aghion et al. 2016) and the impact of various economic factors such as prices of input on the evolution of technology. The problem of potential adverse side effects or even existential risk caused by new technologies has received little to no attention so far. Thus, it appears to be a promising subject to pursue.

Aside from technological progress, which generally gives us more power and more choices, one could also focus on moral and epistemic progress, which improves our ability to make good choices. An example of such research could be the debate on moral convergence towards liberalism (e.g. Cofnas, 2019) and changes via generational replacement.

To learn more, you can check e.g. Links to resources related to progress studies by Patrick Collison; Progress studies reading list by Daniel May; Online course on economics of innovation by Kevin Bryan and Heidi Williams; and blogs The Roots of Progress; Nintil; Kris Gulati’s blog

Who are some of the people already working on this?

Tyler Cowen, Patrick Collison, Pierre Azoulay. Danielle Li, Carolyn Stein, Nicholas Bloom , it might also be useful to check Winners of Emergent Ventures grant (progress studies tranche)

*thanks for building this profile go to Martin Kosik and David Janku

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Improving institutional decision making

#microeconomics #econometrics #behavioral economics #game theory #decision theory

Why is this important?

Large institutions in our societies, most notably governments, have vast resources and power to change the world both, for the better or for the worse. Yet decision processes used in these institutions are often not optimal or rational. If we could improve these processes even by a little, the expected positive value that would be created is very large. However, we often lack knowledge of how to go about improving these processes. Read more here or watch the conference talk below for an introduction.

How to tackle this

Generally, looking into decision making in the group settings would be one option. Specifically, looking into how various methods (like calibration training or structured analytic techniques) improve decisions in real-life scenarios and settings could be valuable. Also, developing better methods for evaluating the quality of arguments when there is no "correct" answer (example 1, example 2, example 3) would be potentially impactful. Another option could be looking into how policy-makers individually work with evidence and update their beliefs (see Vivalt & Coville, 2017 or this blog post, explore whether Kaplan et al., 2016 generalises in policy contexts). Questions like “How to evaluate policy options in data-poor contexts (e.g. future scenarios)? How to run counterfactual policy scenarios taking nonlinearities and feedback loops into account?” might also bring about quite a lot of impact.

Here is a possible framework on how to think about questions related to improving institutional decision making.

See also theresearch directions suggested by the Forethought Foundation.

Who are some of the people already working on this?

Philip Tetlock, Vivalt & Coville; the Simon Institute for Longterm Governance; the Effective Institutions Project; All-Party Parliamentary Group for Future Generations

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Improving health and wellbeing metrics

#health economics #economic evaluation #cost-effectiveness analysis #cost-benefit analysis #behavioural science

Why is this important

The quality-adjusted life-year (QALY) and the disability-adjusted life-year (DALY) are widely used to evaluate healthcare interventions and quantify the burden of disease. Some people also use these metrics informally as a general indicator of value. However, they have a number of major shortcomings in their current form. For example:

  • They focus on a relatively narrow set of health domains, ignoring many other areas of life that matter to us.
  • They normally assess the disutility of health states using preferences of the general public, who tend to be poor at predicting the impact of changes in health on their overall quality of life.
  • They give no weight to positive mental states, beyond the relief of mental or physical illness.
  • They fail to capture the severity of the most horrendous conditions.

For a discussion of some of these issues, see Peasgood, Dolan, & Foster (2019), Brazier & Tsuchiya (2015), Dolan (2008) and Dolan & Kahneman (2008).

The main alternative, often used within central government, is cost-benefit analysis. CBA allows direct comparisons both within and across domains by expressing all outcomes in monetary terms. (See the UK Treasury’s Green Book for an example of this approach.) However, it generally relies on stated or revealed preferences, which are often a poor measure of welfare for a variety of reasons.

These problems lead to serious misallocation of resources in public institutions, such as national governments, and in some non-profit entities as well.

In the conference talk below, Michael Plant and Clare Donaldson of the Happier Lives Institute cover some of the issues with these measures of impact and propose an alternative.

How to tackle this

An alternative metric is the wellbeing-adjusted life-year (WELBY/WALY). This is structurally identical to the QALY but quantifies value in terms of subjective wellbeing (SWB), typically measured using self-reported happiness or life satisfaction.

Existing preliminary research arguably permits the construction and application of a rough WELBY. But further work is required to ensure it fully captures what matters. This includes:

  • Establishing the 'dead' point on SWB scales (the zero point of the WELBY scale): Below what level is it better to be dead?
  • Developing methods for valuing the most severe states: Are the worst states more bad than the best ones are good? How much worse? How can we know this?
  • Establishing the cardinality of the WELBY: How can we ensure a one-point increase represents the same change in welfare on all parts of the scale? Are measures of valence best understood as linear, lognormal, or something else?
  • Choosing a SWB measure: What is wellbeing, and how can it best be measured?

Once this is achieved to some level of satisfaction, the new metric can be used to improve priority-setting. Projects include:

  • Re-estimating the global burden of disease: Which illnesses, injuries and disabilities cause the most unhappiness?
  • Estimating the global burden of unhappiness: Out of all the problems in the world – mental and physical disorders, unemployment, poverty, etc – what accounts for the most disutility?
  • Re-prioritising causes areas and interventions: Which projects are most cost-effective?
  • Comparing human and animal wellbeing: Can the WELBY approach tell us anything about cross-species prioritisation?

For more information on these and many related projects, see:

Who are some of the people already working on this?

A handful of economists have worked specifically on a WELBY for general use, including Paul Frijters, Christian Krekel and Richard Layard. Dozens of others economists have worked on closely related issues, including Andrew Clarke, John Helliwell, Jan De Neve, Nick Powdthavee, Redzo Mujcic, Alois Stutzer and Martijn Burgers. Health economists such as Tessa Peasgood, John Brazier and Paul Dolan have promoted the use of wellbeing in healthcare prioritisation.
*the thanks for building this profile go to Derek Foster

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Other potentially promising directions:

  • Macroeconomic policy (problem profile, research questions) - aside from macro stabilization, long-termism perspective in macroeconomic policy might also be valuable

  • Object-level understanding of Chinese economy and politics / international affairs more generally (problem profile)

  • Labor mobility and immigration (problem profile, blog post)

  • Developmental economics (podcast 1, 2, 3) - example topic 1, 2, 3, 4, 5, 6, 7, 8

If you get interested in any of these topics, let us know. We can:

  • Connect you with researchers working in these fields who can provide feedback on your ideas
  • Help you develop more specific topic ideas
  • Connect you with other students working on the same questions
  • Help you with having your research recognized

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