Writing a final thesis is a big investment, of likely hundreds of hours and a lot of effort. What if you could use this opportunity for something more than just getting your degree? We can support you in using your thesis to learn about, work on and direct your career towards solving the world’s most pressing problems.
There are many problems in the world, and we can't solve all of them due to our limited resources. However, any of us can focus on having the greatest impact possible with the resources available to us. As a student, the resources you have to contribute include your time, effort and skill in research. You may be able to use these resources to contribute to improving the world now, but you can also hone your skills with the aim of increasing your ability to do good in the future. Below we’ll introduce you to our thinking about how you can improve the world as much as possible, focusing on how you can do good with your research.
Our project is based on the principles of Effective Altruism, a movement focused on using high quality evidence and careful reasoning to figure out how to do the most good. It is also informed by the advice of 80000 Hours on how to use your career to significantly improve the world.
We take an impartial, welfarist approach to doing good, meaning we care about the wellbeing of other beings regardless of their location, species, or whether they exist now or will in the future. We are cause neutral, which means we are not pre-committed to focusing on particular problems or possible interventions, but strive to find areas in which we think further research could make a big positive difference. If you don’t share all these views you can still benefit from our work, as you can choose an area we recommend that fits with your personal values.
What are the areas in which we think more research is particularly likely to significantly improve the world? Some of the areas we focus on are long-termism, global catastrophic risk, global health and development and animal welfare, and you will find many topics linked to these areas on our site. We think long-termism (positively influencing the long-term future) is important due to the sheer number of sentient beings that could exist, as well as the lack of attention the future often receives in policy and research areas. Global catastrophic risks are events which would cause major harm on a global scale and potentially increase risk of further harms by destabilising society and slowing progress. We also believe that global health and development and animal welfare are important areas due to their scale and the many ways we can make high impact interventions.
If you want to contribute to solving the world’s most pressing problems, there are a number of strategies you can use. You could have a positive impact through a research career (as explored on our site!), or if you’re interested in considering other careers in which you could improve the world, you can take a look at the 80000 hours website for detailed advice and apply for a career consultancy appointment. For advice on doing good by giving to charity, you can look at the recommendations from GiveWell and Giving What We Can, organisations that carry out thorough research to identify the most effective charities.
If you want to find out more about Effective Altruism, why not join one of the monthly online introductory courses, find a local group near you or sign up to the monthly newsletter to keep up-to-date with community news. You can also take a look at the EA handbook for a more detailed introduction to the core ideas of Effective Altruism.
How useful is it to carefully consider what to focus on with your research if you want to do the most good possible with your research career? How much difference can the problem you choose to work on make to the impact you have? If we were to rank problems by the expected impact of working on them, we would probably anticipate something like the distribution below, where the expected impact of solving different problems increases gradually.
However, research by 80000 hours supports the idea that the impact of solving different problems is distributed more like this:
Some problems are actually many times more impactful to work on than others, with the expected impact differing even by orders of magnitude. You might have ten to a hundred times as high an impact as you otherwise would have done if you choose the most impactful area.
We use a framework proposed by the foundation Open Philanthropy, and further developed by 80000 Hours and the Future of Humanity Institute, to estimate the value of working in particular areas. This is the importance, neglectedness and tractability framework. We look for areas which seem particularly promising according to this framework, and where we think further research specifically could make a significant positive difference, to inform our recommended research directions.
You can also use this framework as a heuristic to help you think about the impact of working on different problems when you’re choosing a topic, bearing in mind that you can contribute to tackling a problem directly with your thesis, but that it may often be best to focus on developing expertise in order to make contributions later. It's good to consider all three criteria, but it could make sense to work on a problem because it scores well on only two criteria — for example, even if there’s only a very small chance a problem is tractable, but it seems very important (meaning there would be a big positive impact if you made progress) and it’s somewhat neglected, it may still be worth working on.
Depending on the stage you are at in your studies, there are various other considerations we recommend you take into account when choosing a focus for your research, such as whether you intend to stay in academia or research long-term, as well as your personal interests and your current level of study. We’ll discuss these other factors later. First, let’s look at importance, neglectedness and tractability in more depth.
Importance refers to the total improvement in welfare, both now and in the future, that we would expect to see if the problem was solved. This may require considering how many sentient beings are or could be affected by the problem and how great the impact on them is. If the problem is an event that is not certain to occur, you can use the concept of expected value to estimate its importance (for example, if there is a 1% chance the event will occur, then its importance is 1% of what it would be if it were certain to occur).
Developing the ability to think independently about how much difference answers to your research questions could make is a particularly valuable skill if you want to make progress in early-stage fields (which are often very interesting and provide opportunities for greater progress and discoveries). This ties into our next consideration: neglectedness.
The criterion of neglectedness attempts to capture how effective it would be to add additional resources and effort to working on a problem. If an area is very well funded and many people are already working in it, you will probably have a bigger impact if you use your time and talent to contribute to a different area, unless you have a very novel approach to tackling the problem. If few people have ever tried to address a problem, however, there may be a lot of low-hanging fruit, and it is less likely that someone else will make progress if you don’t. Choosing a less well-known but potentially very important idea could also raise awareness and encourage more people to research it further.
An area might be neglected because it doesn’t offer much financial reward, political incentives are missing, it’s low visibility, or it’s considered low status. Newer fields, areas where new techniques are emerging, and intersections between academic fields are more likely to be neglected areas.
While it can be very valuable to work in neglected areas, depending on your career goals, it may also be useful to consider whether an unpopular topic may damage your career capital, and to keep this in mind when choosing a research question. It’s also worth bearing in mind that if few people are working on an important problem, it may be because it has already been established that progress will be very hard to make. This brings us to our last consideration: tractability.
The last criterion to consider is the tractability of the problem; with more research, would it be possible to make progress? When choosing your thesis topic, it makes sense to consider both whether the problem seems tractable in general and also whether you are a good fit to work on it at this point. If you can think of a neglected and important topic but have no idea how you would go about researching it (even after using our coaching service and talking to people working in the relevant area), it might not be the right question for your thesis.
More broadly, when considering how tractable a problem is it's good to follow the evidence — has anyone made any progress already? How much if so? It can help to listen to what researchers and communities connected to this area think it’s valuable to work on, making sure you pay close attention to their reasoning. However, you might not find this evidence if the problem is very neglected. In that case, it makes sense to try to create some evidence by doing some preliminary work on the problem if it is promising on the other dimensions.
Although all else equal we think it is valuable to seek a problem that scores highly on a combination of tractability, neglectedness and importance, there are other factors we believe it is important to take into account, such as whether you’re doing an undergraduate, master’s or PhD and what your long term career plans are. Our ideas on research careers are inspired by the 80000 hours’ article on how to do high impact research. Before continuing, if you’re not sure about your long-term career plans you might find it useful to assess whether you’re a good fit for a career in research.
First, we’ll discuss what might be a good strategy if you’re an undergraduate or master’s student and plan to pursue a research-heavy career. We’ll then explore how to make your thesis as impactful as possible if you plan to pursue a career outside of academia. Finally, we’ll explore how finding a secondary supervisor outside of academia, if your university allows this, might be useful for building your career capital.
If you’re considering pursuing a research career in future, whether in academia or in an organisation outside academia, you should make building your research skills a priority. In order to have a substantial impact, your research will need to be of excellent quality. There are several ways you can improve your research skills. Aside from working on your thesis, consider joining an already established research group or project at your department and attending summer research programmes. You might find some of our online resources helpful, such as our Tips on Doing Impactful Research. When choosing your thesis topic, consider using methods which will push you to develop your skills. You should try to choose a skilled supervisor with a good reputation, as getting high-quality guidance and helpful feedback will help you build your research skills. The primary goal of your thesis at this stage is not to come up with new findings, but rather to develop your skills and test your fit for research.
You can learn more about what an academic career is like and whether this path would be a good fit for you here.
Ideally, you will be able to build your research skills while pursuing directions that seem highly valuable in order to learn more about them and make it easier to contribute later. However, if you can’t find a great supervisor who can help you hone your research skills in one of these directions, you should choose an area that allows for greater skill-building, and come back to more valuable directions at a later stage. You will likely have a chance to switch topics and start focusing on a topic which is likely to have a higher impact when you choose the focus of your PhD.
If you don’t expect to pursue a research career, you can still use your thesis to improve the world by focusing on a particularly important problem and using your thesis to learn more about it, with the aim of working on this problem later in your career. If this is your goal, you should optimise for gaining a more thorough understanding of the problem and of actionable ways to tackle it. Also check out the section below this one, to learn more about using your thesis to build a relationship with an organisation you might want to work for in the future.
There are other ways to use a career outside of academia to contribute to solving the world’s most important problems. Some people apply for particularly high paying jobs and help solve social problems by donating a significant portion of their salaries to effective charities and enterprises. If this is the path you’re most interested in following, optimising your thesis for improving your chances of getting a higher paying job after your studies may be the most valuable option.
Whether you are interested in a research career outside of academia (e.g. at a think tank) or a non-research career, you could build career capital by finding someone from an organisation you’d like to work for who will act as your thesis supervisor, and choosing a topic that will help that organisation’s work in some way. If your university allows this, it can enable you to provide strong evidence that you have the aptitudes the organisation is interested in, which can be difficult to demonstrate during one interview. Making connections is also the best way to get a job — much better than sending out CVs. To find an industry supervisor, consider asking your university or academic supervisor whether they can connect you. If there are alumni of your university at the company you’re interested in, you could connect via LinkedIn and ask what they think the company would appreciate being researched and whether they are able to introduce you to anyone else at the organisation. They may be more willing to help as you already have something in common and it’s an opportunity for them to mediate their organisation benefitting from your research.
If you want to prioritise learning quickly you may want to look either for organisations that have reputations for particularly high performance or growing start-ups. Alternatively, choosing a large, well-known organisation may be the best choice if you want to prioritise building your credentials.
If you can’t find a supervisor who works for an organisation you’re interested in, finding a thesis topic that seems very relevant for a specific organisation or for many organisations may still facilitate you reaching out to them later. They will also see your thesis topic on your CV if you apply in future. To find relevant topics, aside from researching the organisation(s) as thoroughly as possible, you could consider questions such as: ‘What are the most pressing questions in this field?;’ ‘Which questions are considered solved and which lack solutions?;’ ‘Are there any new trends appearing in the literature? What do they suggest about the future development of the field?;’ ‘What are the best experts’ guesses on how the field will develop in future?’ However, bear in mind that developments in your academic field won’t always relate to the research that organisations will find most useful. As finding a thesis topic that organisations will be interested in without connecting with them requires more guesswork, it’s preferable if you are able to connect with an organisation before choosing your thesis topic.
If you plan to stay in academia, developing a strong publications record early is very important due to the high levels of competition. Getting great training is also important. Aside from working on your thesis, you could also apply for research internships, such as the Junior Research Programme in psychology at the University of Cambridge. These will build your research skills via mentorship and collaborative research projects ending with publication, sometimes in very prestigious journals.
When choosing your thesis topic, it may be best to seek out the most impressive supervisor you can find, even if they don’t operate in the area you’d ideally work in long-term, and to choose a thesis topic that will have the highest chance of being published in the best journal. One way of establishing what this topic might be is to ask for the opinions of your potential supervisors. The other way is to look at what the best journals usually publish. For example, top economics and philosophy journals are known to publish mainly highly theoretical work.
However, it’s also good to consider how much your topic choice will lock you into a specific subfield. In our experience, the lock-in effect is stronger in some disciplines (e.g. economics, psychology, engineering) and less strong in others (e.g. life sciences, philosophy). To figure out how much of a lock-in effect there is in your discipline, try asking more experienced researchers in the field as well as observing whether you see people in your discipline changing focus. If you find that there is a good chance of becoming locked-in to a specific field, it’s much more important to choose a topic that will both be publishable in the best journals and will also be valuable and important to focus on from the perspective of improving the world. We can help you with finding such a topic.
If you want to build a research career in academia, in many disciplines you should focus on making theoretical contributions (e.g. exploring what drives people in general; how a specific type of system works; theoretical models we can use to understand the world better) rather than applied research (e.g. the effectiveness of specific interventions). However, applied research experience might be an advantage if you want to do research outside of academia (e.g. in think tanks, nonprofits, or international organisations). If you’re thinking of pursuing a research career outside of academia, bear in mind that it might be harmful to leave academia if you want to re-enter in future.
Research positions outside of academia can be more fulfilling because your work has a more tangible impact and will involve more teamwork. These are positions within international organisations (e.g. The World Bank); think tanks; companies that develop important technology (e.g. Gilead Sciences which developed drugs to treat HIV and Hepatitis, and Tesla which is developing cheaper batteries); data science within businesses, and finally non-traditional academia, such as work funded by 2-4 year grants with no teaching load (e.g. at the Future of Humanity Institute in Oxford).
If you’ve already established your career with previous publications, your field doesn’t require such a strong publications track record or you’re planning to work as a researcher outside of academia, you can probably focus more heavily on simply choosing a research direction you expect to be high impact.
We’ve covered the value of thinking about the importance, tractability and neglectedness of a problem, as well as how your future career plans and your current level of study may influence your choice of research direction. We think the factors below are also worth considering:
All else equal, we think it is good to select a research topic based on your interests, as you’re much more likely to be motivated and successful at researching a topic if you are genuinely enjoying it. Your skill at research will be a powerful intellectual tool in future, so it’s worth choosing a topic that really motivates you to develop it.
However, it is also the case that your interests may change and you may discover an interest you didn’t anticipate if you spend some time exploring. Moreover, there can be other sources of motivation aside from your interests. If working on your thesis may actually help you to land a job or help an organisation with what they need, this could also be a great motivator. Research from 80000 Hours also shows you can become passionate about work you never would have predicted finding motivating in the right conditions.
We also think it’s important to take your personal fit into account. Even if a topic seems like it could be high impact to pursue, is it a good fit for your skills? It’s often good to spend time testing your fit with a project, rather than fully committing to something right away. You might find that you are most suited to a particular sort of research, and often the best way to find this out is through practice. It’s also valuable to draw on your own intuitions and knowledge of yourself to determine whether you would be a good fit for an area. For help identifying your personal strengths, take a look at this article by 80000 Hours.
As the most successful researchers have far more impact than the rest, entering a field in which you’re near the top 10% most successful researchers could easily increase your expected impact more than 10 times compared to if you’d entered or remained in a field in which you would have been a median researcher.
Finally, although some topics have the potential to have much higher impact than others, it may be that your comparative advantage is in a direction Effective Thesis doesn’t currently consider a priority. If you think you might be an unusually good fit, researching this topic could be your highest impact option. However, if you think that you could be a fit for one of our priority topics, we would encourage trying this first.
Please keep in mind that although these ideas stem from evidence-based career advice, we haven’t yet evaluated all our advice. We welcome suggestions for how this advice could be improved and feedback on what worked for you.
We hope these key ideas have given you a clear understanding of Effective Thesis’ goals and that you enjoy exploring the rest of the site. We’ve compiled a list of topics we think are particularly high impact across a wide range of fields, including economics, computer science, philosophy, engineering, business, history and law. The research agendas of organisations working on pressing problems can also be a good starting place to find a research topic – we’ve compiled a list here. For a list of further information including online courses, tools, funding and competitions, take a look at our Resources page.
If you want to use your thesis topic to work on some of the world’s most pressing problems, we’d love to help. Our coaching service can guide you through the process of finding a focus for your thesis as well as connecting you to a network of other researchers working on these questions. We will pair you with a coach who’s a good fit for your work, and together you can identify the most important problems in your area and how your research could help fix them.
Alternatively, if you’re not currently interested in coaching, you can still sign up for our database of potential supervisors and our fortnightly opportunities search email, which will send you news of internships, jobs, funding, prizes and other information relevant to early career researchers.
If you’re interested in collaborating with us, check out opportunities to do so here. If you have any questions or feedback, please don’t hesitate to contact us.
Thanks to Elinor Clark for help with writing and editing these pages.