Writing a final thesis is a big investment, of likely hundreds of hours and lots of effort. What if you could use this opportunity for something more than just getting your degree? We can support you to use 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 possible positive impact with the resources available to us. As a student, the resources you have to contribute include your time and effort and your skill in research. You may be able to use these to contribute to improving the world now, and you can also direct your time and effort to honing your skills to do even more good in the future. Below we’ll introduce you to more of our thinking on how you can use the resources you have to do as much good as possible. We’ll start with a brief overview of Effective Altruism, which is a set of principles that underlies or work. After that we’ll explore how your level of study and other personal factors might inform the way you choose to do good.
Our project is based on the principles of Effective Altruism, specifically ideas about how to use your resources 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.
Many people want to make a positive difference, but it can be hard to know how to go about doing this. That’s where Effective Altruism comes in. Founded in 2009 by philosophers Toby Ord and William MacAskill, Effective Altruism is a supportive community of people using high-quality evidence and careful reasoning to work out how to help others as much as possible. Some of these ways can be quite surprising and you can do a lot more good than you might realise.
Effective Altruism suggests taking an impartial, welfarist approach to doing good. The impartial part challenges us to expand the group of beings we care about beyond national, species and generational borders, and a welfarist approach means focusing firstly on improving well-being. This involves carefully analysing which interventions and causes are actually having or are expected to have the highest impact in terms of improving welfare, and stepping beyond our biases to work on these.
So what are the world’s most pressing problems? Some of the areas Effective Altruists focus on are long-termism, global health and development and animal welfare. Long-termism seems particularly high impact due to the sheer number of sentient beings that could exist in the future, as well as the lack of attention the future often receives in policy and research areas. Global health and development and animal welfare are also 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, Effective Altruism highlights 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 how to donate to the most effective charities, you could look at the Give Well top charities and the Giving What We Can recommendations.
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 ideas of Effective Altruism.
Firstly, how much might you be able to increase the good you do by carefully considering what to focus on with your research? 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.
If you’re interested in using your thesis to do as much good as possible, you’re probably wondering how to go about choosing a research topic that’s likely to have a particularly positive impact.
A framework sometimes used by organisations aligned with Effective Altruism to estimate the value of working in a particular area is the importance, neglectedness and tractability framework. We look for areas which seem particularly promising according to this framework, and in which we think further research could make a positive difference, to inform our recommended research directions.
You can use this framework as a heuristic to think about working on the impact of working on different problems yourself when you’re choosing a topic. 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, if there would be a huge positive impact if you could make 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.
Importance refers to the total improvement in welfare, both now and in the future, 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 is. If the problem is an event that is not certain to occur, you can use the concept of expected value to determine 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).
Try to think from an impartial and cause-neutral perspective about how much good progress in your research area would create, 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 the area in order to make contributions later. 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 be able to 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.
It might be that an area is 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 and areas where new techniques are emerging, and intersections between academic fields, are also more likely to be neglected areas.
While it can be very valuable to work in unfairly 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 a 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, does it seem like it would 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. When picking a topic, think about practical strategies for how you would approach it and whether you can think of a concrete, manageable question. If the topic is too broad, it may be harder to do useful research on it.
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 prominent 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 focus on a problem that scores highly on a combination of tractability, neglectedness and importance, there are other factors we believe are important to consider, 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 in future. We’ll then explore how to make your thesis as impactful as possible if you plan to pursue a a career outside of research.
If you’re considering pursuing a research career in future, whether in academia or with an organisation outside it, 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. Some of our online resources might also be helpful, such as our Tips on Doing Impactful Research. When making a final decision on your thesis topic, consider using methods which will push you to develop your skills. You should also make sure 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 one of the problems that seem most important and using your thesis to learn more about it, with the aim of doing direct work 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.
If you want a non-research career working on pressing problems, 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 them 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 you as you already have something in common and because 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 have the opportunity to achieve something impressive like founding a start-up and can use your thesis to help you, this is another option to consider. However, if your chances aren’t especially strong, it might make sense to use your thesis to pursue more reliable ways of building career capital.
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 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 what research organisations will find most useful. As finding a thesis topic that organisations will be very 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.
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.
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. 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. 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.
We suggest choosing 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 probably 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 might 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; Tesla which is developing cheaper batteries), data science within businesses or non-traditional academia – work in academia funded by 2-4 year grants with no teaching load (e.g. the Future of Humanity Institute in Oxford).
If you’ve already established your career with your 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 also find an interesting topic you didn’t think of as a candidate before 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 do 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.