Owen Cotton-Barratt: Lead Researcher, Global Priorities Project
Katja Grace: Research Assistant, Machine Intelligence Research Institute
This is a summary made by Katja of points made by Owen during a conversation on March 24 2014.
What the Global Priorities Project (GPP) does
The Global Priorities Project is new, and intends to experiment for a while with different types of projects and then work on those that appear highest value in the longer term. Their work will likely address questions about how to prioritize, improve arguments around different options, and will produce recommendations. It will probably be mostly research, but also include for instance some policy lobbying. They will likely do some work with concrete policy-relevant consequences and also some work on general high level arguments that apply to many things. Most features of the project are open to modification after early experimentation. There will be principally two audiences: policy makers and philanthropists, the latter including effective altruists and foundations. GPP has some access to moderately senior government and civil service policy people and are experimenting with the difficulty of pushing for high impact policies.
Research topics will be driven by a combination of importance and comparative advantage. GPP is likely to focus on prioritizing broad areas rather than narrower interventions, though these things are closely linked. It is good to keep an eye on object level questions to ensure that you are thinking about things the right way. Owen is interested in developing frameworks for comparing things. This can produce value both in their own evaluations and through introducing metrics that others want to use, and so making proposals more comparable in general.
Work so far
Unprecedented technological risks
GPP has a draft report on unprecedented technological risks. They have shown it to several people involved in policy and received positive feedback. Somebody requested a stack of printed copies for their office, to hand out to people.
How to evaluate projects in ignorance of their difficulty
Owen is working on a paper about estimating returns from projects where we have little idea how difficult they are. Many research tasks seem to fall into this category. For instance, ‘how much money we should be putting into nuclear fusion?’ We have some idea of how good it would be, and not much idea of how hard it is. But we are forced to make decisions about this, so we make an implicit statement about likelihoods. But while it is implicit, we may get it wrong sometimes.
Short term changes
In the short time GPP has existed, it has moved to focus less on policy, because experimenting with others things seemed valuable.
Views on methodology
Long run effects
It has been suggested by others that research on long run consequences of policies is prohibitively difficult. Owen believes that improving our predictions in expectation about these long run consequences is hard but feasible. This is partly because our predictions are currently fairly bad.
There are already some informal arguments in the community surrounding GPP about long run implications which it would be good to write up. For instance, there is an argument that human welfare improvements will tend to be better than animal welfare improvements in the long run, because the former have benefits which compounds over time, while animal welfare does not appear to. This is a good case where short term benefits predictably decouple from long term benefits, while in other cases short term benefits may be a reasonable proxy.
GPP will likely focus on long run effects to some extent, but not solely. Owen believes they are very important. However he also thinks routes to impact involve bringing people on board with the general methodology of prioritization, and more speculative research is less persuasive. He thinks people interested in prioritization tend to think long run impacts dominate the value of interventions, but focusing there too strongly will cause others to write us off. He also thinks that we will ultimately need to use some short-term proxies for long term benefits.
Owen is in favor of a relatively high degree of quantification in this kind of research. However this has caveats, and he advocates awareness of possible dangers of quantification. We can be too trusting of the numbers produced in this way. We should be careful about models. Sometimes it is better to throw up our hands and say ‘we don’t know how to model this’ and give some qualitative considerations than proceeding with a bad model. For long term effects, we are at that stage where the best quantified models may be worse than qualitative arguments. However we should be working toward quantification. One benefit of quantification is that it improves conversations and truth seeking. Even before you know how to model a process, if you make explicit models then you can have explicit conversations with people about the models, and about what’s wrong with them or not.
Risks with quantification
Quantification is a natural tool if we want to make comparisons. If we want a shallow picture of what is going on, it is not clear that quantification will be useful.
Trying to break down intuitions into further details can make things worse. You can miss out factors and be unaware of the omission. You can pay too much attention to factors because you put them in your model, or disregard factors because you didn’t. You can confuse people into thinking you are more confident than you are. You can be duped by thinking you have a formula. Many people are quite bad at quantification, which makes it worse to advocate it in general. Then there are simple time costs: explicit quantification is time consuming.
Nonetheless, for questions we are interested in, Owen thinks it is important to try.
Methodological change and progress
GPP hopes to make methodological progress that will be applicable to any decisions. For instance their current work on evaluation under uncertainty about costs arose from their own work on unprecedented technological risks. After they have developed a general methodology there, they can try to apply it to further problems. Back and forth between concrete prioritization and abstract general questions is likely to characterize the work.
It seems generally useful when looking at more high level questions to pay attention to concrete cases, to check that your thinking is applicable and reasonable there.
The project currently uses much of Owen’s time and a small amount of several others’ time, perhaps summing to around one and a half full time people. It’s hard to estimate, because some of the meetings that involve other people would probably occur if GPP didn’t exist, under another project. Having a label probably makes somewhat more of these things happen. Niel Bowerman has has been putting a nontrivial fraction of his time into it, but he will be cutting back to work on outreach.
The expenses of the organization are largely about one person’s worth of employment, plus some overheads in terms of office rent and sharing administrative staff. Some of the work comes from people being employed by FHI.
Where is the value of cause prioritization in general?
Owen is optimistic about cause prioritization, because it is neglected, and obviously important.
Current best guesses vs. best
Owen thinks there is quite a large range of cost effectiveness between different things, but not absolutely enormous.
Finding new best interventions vs. marginally improving a lot of good spending
There are different routes to impact with cause prioritization. Owen thinks a major route to impact is through laying bricks of prioritisation methodology. This will help people in the future to do better prioritisation (and could be better than anything we manage in the near-term future).
Among direct effects on funding allocation, there are also substantially different kinds of impact you might hope for. You can uncover new very high impact interventions, and do them. Or you can just get a group of people who are currently doing quite good things with their money to do better things with their money. Owen is slightly more optimistic about the latter, but fairly uncertain.
Object vs. meta level research
Prioritization work should be focused in the short term on a mixture of object level research output and methodological progress. GPP’s time will be split fairly evenly between them, perhaps leaning toward the methodological. It can be hard to work on methodology without engaging with more concrete questions.
Why do others neglect cause prioritization?
Owen’s best explanations for the neglect of cause prioritization research in general are that it’s hard, that it’s hard to evaluate, and that academic incentives for research topic choice are not socially optimal. Also, like most research, its costs are concentrated while its benefits are distributed.
The term ’cause prioritization’ seems suboptimal to Owen, and also to others. Sometimes it is good, but it is used more broadly than how people have traditionally thought of ’causes’ and confuses people. It is also confusing because people think it is about causation. Owen would sometimes talk about ‘intervention areas’. He doesn’t have a good solution in general, but thinks we should be more actively looking for better terms.
Routes to contributing to prioritization
Thoughts on other organizations
Overall Owen thinks the entire area is under-resourced, so it’s great when other people are working on it. Even unsuccessful work will be valuable as it helps us to learn what works.
Owen thinks GiveWell Labs is laying a lot of useful groundwork for prioritization work. The ‘shallow investigations’ they have been focusing on so far have their value in aggregating knowledge about causes, by researching the funding landscape, who is working on problems, and what is broadly being done. This knowledge base can then be used by anyone who is thinking about cause prioritization, whether in GiveWell Labs or outside. So there are big positive externalities from making the in-progress research public.
GiveWell Labs haven’t yet turned this broad knowledge of existing work into comparisons between areas or prioritization between them. Owen is keen to see what their approach will be.
Leverage are probably doing some prioritization research, which may be very valuable. So far, however, they haven’t published much. Owen would love to see more of their analysis. Communicating is a cost, but not communicating bears the risk that research will be duplicated elsewhere or that things they discover won’t be built upon.
Copenhagen Consensus Centre
Owen is a big fan of the work the CCC does. They essentially represent expert economic opinion on global prioritisation.
There are a few reasons not to simply use their conclusions. The cost-benefit analysis which underlies most of their recommendations can in some cases miss important indirect effects. They don’t have a methodology which is strong at evaluating speculative work. And their recommendations are from the stance of global policy, which may not be directly applicable to altruists or even national policy-makers. However, their work remains one of the best resources we have today.
GPP would welcome more funding. It would spend additional money securing the future of the project and hiring more researchers. It’s not clear how hard it is to attract good researchers, as they do not have the funds to hire another person yet, so have not advertised. At the moment money is the limiting factor in scaling up this research.
They would hire people who would similarly work on a variety of small-scale projects which seem important. According to skills they might work more directly on research or on using the research to leverage additional attention and work from the wider community. They would also be interested in hiring someone with more policy expertise. Owen has looked at this a bit, but it is probably not his comparative advantage.
Other conceivable projects
Influencing foundation giving
There are projects to get foundations to share more of their internal research, such as Glasspockets and IssueLab. Since small amounts of prioritization are done inside foundations, one could try to get these sharing efforts to focus more on sharing prioritization research. This sort of project has occurred to Owen in the past, but since these projects (e.g. Glasspockets) are already doing something like this, it doesn’t seem that neglected, so he thought it is probably not the high impact opportunity. Also, what the foundations are doing is likely not what we are thinking of when we say ’cause prioritization’. They pick an area to focus on, then sometimes try to prioritize based on cost effectiveness within that area.
In response to the suggestion that it is best to focus on getting funders to care about prioritization, Owen thinks that may be true one day, but we first need higher quality research to be persuasive.
Another approach to influencing foundation giving is to get people who think about prioritization the right way into the foundations.
It might be valuable to try to get cause prioritization taken up within academia, and seen as an academically respectable thing to do. This would help both with making the conclusions look more respectable, and in getting more brainpower from the class of people who would like to work at universities.
Who else does things like this?
The economics profession
We should think of academic economics as a part of the reference class of cause prioritization. A lot of economics focuses on long term effects of things. Economists would think of themselves as the experts on how to prioritize things, fairly justifiably. They have a lot of knowledge, which Owen tries to be broadly familiar with.
Owen thinks despite the fact that economists do a lot of relevant work, they tend not to actually produce prioritization of causes. So there may be a large backlog of relevant work to use in prioritizing causes. Owen has some idea of the landscape, though an imperfect one. He thinks it would be great to get more economists working in the area.