Why "cause area" as the unit of analysis?
post by riceissa
This is a question post.
Back in April 2018, I spent some time trying to understand the hierarchy/structure/classification of cause areas. I did this at the suggestion of Vipul Naik [EA · GW], who wanted to (1) categorize cause areas treated on the Cause Prioritization Wiki so that there was more structure to it than that of a jumble of 100+ cause areas, and (2) make the analysis of cause areas more systematic. (I believe he was also interested in this because the Donations List Website [EA · GW] that he created also needed a better ontology of cause areas.)
Some of the outputs of that investigation are:
I came away from the above investigation feeling pretty confused about the nature of cause areas. Given just a description of reality, it didn't seem obvious to me to carve things out into "cause areas" and to take "cause area" as the basic unit of analysis/prioritization (which is what cause prioritization is all about).
Some thoughts/intuitions that contribute to this feeling are:
- As explained (EA Forum link [EA · GW]; HT Edo Arad) by Owen Cotton-Barratt back in 2014, there are at least two meanings of "cause area". My impression is that since then, effective altruists have not really distinguished between these different meanings, which suggests to me that some combination of the following things are happening: (1) the distinction isn't too important in practice; (2) people are using "cause area" as a shorthand for something like "the established cause areas in effective altruism, plus some extra hard-to-specify stuff"; (3) people are confused about what a "cause area" even is, but lack the metacognitive abilities to notice this.
- A cause area can try to "seem" big or small by lumping together more and more things in the world (or alternatively excluding more things from itself). Do we compare "animal welfare improvement" against "agent foundations research", or against "technical AI safety work", or against "technical, strategy, or policy work in AI safety", or against "existential risk reduction", or against "applied mathematics related to futuristic technology"?
- More generally, if we take some basic unit of action like "1 person-year of work" then we can form sets of actions and call those sets "cause areas" (these sets don't necessarily form a partition, i.e. there might be actions contained in multiple causes and actions not contained in any cause). But then we can imagine defining some arbitrary "cause area" that just picks out the most high-value actions and declares it "the most important cause". Of course, finding which actions are contained in this "most important cause" would be difficult, and the task of cause prioritization would seem to be reduced to this search process.
- I can imagine an argument taking place where the opponent of a cause area picks some ineffective actions within the cause area while a supporter picks effective actions, so they disagree regrading the overall effectiveness of the cause area despite agreeing about the effectiveness of specific actions. Maybe even a motte-and-bailey argument where the supporter draws a tighter boundary around the cause when attacked, and loosens the boundary at other times to be able to call their preferred interventions effective. (I don't actually know if such arguments are taking place, so this is just a theoretical concern at the moment.)
- One way looking at cause areas might be useful is from an evaluator's perspective of "what skills/domain expertise do I need to be able to evaluate specific programs/research topics?" If skillsets tend to "unlock" a bunch of potential programs at once, then there might be a natural-seeming boundary around these programs, which might correspond to our intuitive notion of cause area. But this seems to depend on the order in which various skills are acquired. To take an extreme case, if someone had a lot of domain-specific expertise in many domains but lacked some general skill (like generalist research skills, knowledge of statistics, programming experience) then by learning the general skill they suddenly "unlock" a whole bunch of "cause areas" at once.
- I think reductionism and "dissolving the question [LW · GW]" type moves have been useful in many situations, and I have a vague intuition that the notion of cause area can be reduced in some way.
- In practice, Open Philanthropy Project (which is apparently doing cause prioritization) has fixed a list of cause areas, and is prioritizing among much more specific opportunities within those cause areas. (I'm actually less sure about this as of 2021, since Open Phil seems to have made at least one recent hire specifically for cause prioritization.)
- I've noticed that as I learn more about a cause area, I get more opinionated about activities within it. A naive analysis cannot distinguish effectiveness within a cause area, and instead puts a uniform score over the whole cause area, whereas a more sophisticated analysis puts precise scores over each action within a cause area. So it feels like "cause prioritization" is just a first step, and by the end it might not even matter what cause areas are. It seems like what actually matters is producing a list of individual tasks ranked by how effective they are.
- In this 80,000 Hours podcast episode Toby Ord talks about the idea of risk factors, as distinguished from risks. This seems to further complicate the situation.
- Some recent Katja Grace posts that are relevant and that make me even more confused: Are the consequences of groups usually highly contingent on their details? and Infinite possibilities.
Why does any of this matter? Here are a couple of reasons that come to mind:
- Practically, projects like Cause Prioritization Wiki, Donations List Website, and other efforts [EA · GW] to categorize cause areas require some organization system that makes sense.
- From a more philosophical or emotional perspective, I feel dissatisfied with my current understanding.
- In terms of public discourse, people are actually using the concept of "cause area" to do further thinking. If the idea of a cause area is not a reliable one, then all of this further thinking is done on a shaky foundation, which seems worrying. I feel like these [EA(p) · GW(p)] two [EA(p) · GW(p)] comments by Buck Shlegeris and this post by Katja Grace are possibly doing this thing, or giving less careful thinkers the idea that this is a sound move.
I am curious to hear people's thoughts on this. I would also appreciate pointers to existing discussions (I feel like I've been paying attention, but it seems plausible to me that I've missed some).
Thanks to Vipul Naik for funding part of my work on this post, and for funding my work on cause areas that led to this post. Thanks also to Edo Arad for pushing me to finish this post.
answer by MichaelPlant
) · GW
FWIW, I think it helps to think of effective altruism along the following lines. This is more or less taken from chapters 5 and 6 of my PhD thesis which got stuck into all this in tedious (and, in the end, rather futile) depth.
Who? As in, who are the beneficiary groups?
Options: people (in the near-term), animals (in the near-term), future sentient life
What? As in, what are the problems?
This gives you your cause areas, i.e. the problems you want to solve that directly benefit a particular group, e.g. poverty, factory farming, X-risks.
Effective altruism is a practical project, ultimately concerned about what the best actions are. To solve a problem requires thinking, at least implicitly, about particular solutions to those problems, so I think it's basically a nonsense to try to compare "cause areas" without reference to specific things you can do, aka solutions. Hence, when we say we're comparing "cause areas" what we are really doing is assessing the best solution in each cause area "bucket" and evaluating their cost-effectiveness. The most important cause = the one with the very most cost-effective intervention.
How? As if, how can the problems be best solved?
Here, I think it helps to distinguish between interventions and barriers. Interventions are the thing you do that ultimately solve the problem, e.g, cash transfers and bednets for helping those in poverty. You can then ask what are the barriers, i.e. the things that stop those interventions from being delivered. Is it because people don't know about it? Do they want them but can't afford them, etc? A solution removes a particular barrier to a particular intervention, e.g. just provides a bednet.
What's confusing is where to fit in things like "improving rationality of decision-makers" and "growing the EA movement", which people sometimes call causes. I think of these as 'meta-causes' because they indirect and diffusely work to remove the barrier to many of the 'primary causes', e.g. poverty.
It's not clear we need answers to the 'why?', 'when?', and 'where?' queries. Like I say, if you want to waste an hour or two, I slog through these issues in my thesis.
comment by MichaelA ·
2021-01-26T23:56:21.302Z · EA(p) · GW(p)
I like this answer.
I think it's basically a nonsense to try to compare "cause areas" without reference to specific things you can do, aka solutions. Hence, when we say we're comparing "cause areas" what we are really doing is assessing the best solution in each cause area "bucket" and evaluating their cost-effectiveness. The most important cause = the one with the very most cost-effective intervention.
Maybe a minor point, but I don't think this is quite right, because:
- I don't think we know what the best solution in each "bucket" is
- I don't think we have to in order to make educated guesses about which cause area will have the best solution, or will have the best "identifiable positive outliers" (or mean, or median, or upper quartile, or something like that)
- I don't think we only care about the best solution; I think we also care about other identifiable positive outliers. Reasons for that include the facts that:
- we may be able to allocate enough resources to an area that the best would no longer be the best on the margin
- some people may be sufficiently better fits for something else that that's the best thing for them to do
- (And there are probably cases in which we have to or should "invest" in a cause area in a general way, not just invest in one specific intervention. So it's useful to know which cause area will be able to best use a large chunk of a certain type of resources, not just which cause area contains the one intervention that is most cost-effective given generic resources on the current margin.)
For example, let's suppose for the sake of discussion that technical AI safety research is the best solution within the x-risk cause area, that deworming is the best solution in the global health & development cause area, and that technical AI safety is better than deworming. In that case, in comparing the cause areas (to inform decisions like what skills EAs should skill up in, what networks we should build, what careers people should pursue, and where money should go), it would still be useful to know what the other frontrunner solutions are, and how they compare across cause areas.
(Maybe you go into all that and more in your thesis, and just simplified a bit in your comment.)
 The fact that this is a reply to you made it salient to me that the term "global health & development" doesn't clearly highlight the "wellbeing" angle. Would you call Happier Lives Institute's cause area "global wellbeing"?
 Personally, I believe the third claim, and am more agnostic about the other two, but this is just an example.
answer by MichaelA
) · GW
My main thoughts on this:
- I share the view that EAs often seem unclear about precisely what they mean by "cause area", and that it seems like there are multiple somewhat different meanings floating around
- This also therefore makes "cause prioritisation" a somewhat murky term as well
- I think it would probably be valuable for some EAs to spend a bit more time thinking about and/or explaining what they mean by "cause area"
- I personally think about cause areas mostly in terms of a few broad cause areas which describe what class of beneficiaries one is aiming to help
- If future beings: Longtermism
- If nonhuman animals (especially those in the near-term): Animal welfare
- If people in developing countries: Global health & development
- We can then subdivide those cause areas into narrower cause areas (e.g. human-centric longtermism vs animal-inclusive longtermism [EA · GW]; farm animal welfare vs wild animal welfare)
- This is somewhat similar to Owen Cotton-Barratt's "A goal, something we might devote resources towards optimising"
- But I think "a goal" makes it much less clear how granular we're being (e.g., that could mean there's a whole cause area just for "get more academics to think about AI safety"), compared to "class of beneficiaries"
- There are also possibilities other than those 3
- e.g., near-term humans in the developed world
- And there are also things I might normally "cause areas" that aren't sufficiently distinguished just by the class of beneficiaries one aims to help
- e.g., longevity/anti-ageing
- I don't mean to imply that broad cause areas are just a matter of a person's views on moral patienthood; that's not the only factor influencing which class of beneficiaries one focuses on helping
- E.g., two people might agree that it's probably good to help both future humans and chickens, but disagree about empirical questions like the current level of x-risk, or about methodological/epistemological questions like how much weight to place on chains of reasonings (e.g., the astronomical waste argument) vs empirical evidence
- I'm very confident that it's useful to have the concept of "cause areas", to sometimes carve up the space of all possible altruistic goals into at least the above 3 cause areas, and to sometimes have the standard sorts of cause prioritisation research and discussion
- I think the above-mentioned concept of "cause areas" should obviously not be the only unit of analysis
- E.g., I think most EAs should spend most of their lifetime altruistic efforts prioritising and acting within broad cause areas like longtermism or animal welfare
- E.g., deciding whether to work on reducing risks of extinction, reducing other existential risks, or improving the longterm future in other ways
- And also much narrower decisions, like precisely how best to craft and implement some specific nuclear security policy
I'll add some further thoughts as replies to this answer.
comment by MichaelA ·
2021-01-26T05:35:46.845Z · EA(p) · GW(p)
[I think the following comment sounds like I'm disagreeing with you, but I'm not sure whether/how much we really have different views, as opposed to just framing and emphasising things differently.]
So it feels like "cause prioritization" is just a first step, and by the end it might not even matter what cause areas are. It seems like what actually matters is producing a list of individual tasks ranked by how effective they are.
I agree that cause prioritization is just a first step. But it seems to me like a really useful first step.
It seems to me like it'd be very difficult, inefficient, and/or unsuccessful to try to produce a ranked list of individual tasks without first narrowing our search down by something like "cause area" seems like it'd be wildly impractical. And the concept of "cause area" also seems useful to organise our work and help people find other people who might have related knowledge, values, goals, etc.
To illustrate: I think it's a good idea for most EAs to:
- Early on, spend some significant amount of time (let's say 10 hours-1,000 hours) thinking about considerations relevant to which broad cause area to prioritise
- E.g., the neglectedness of efforts to improve lives in developing vs developed countries countries, the astronomical waste argument, arguments about the sentience or lack thereof of nonhuman animals
- Then gradually move to focusing more on considerations relevant to prioritising and "actually acting" within a broad cause area, as well as focusing more on "actually acting"
And I think it'd be a much less good idea for most EAs to:
- Start out brainstorming a list of tasks that might be impactful without having been exposed to any considerations about how the scale, tractability, and neglectedness of improving wellbeing among future beings compares to that of improving wellbeing among nonhumans etc.
- What would guide this brainstorming?
- I expect by default this would involve mostly thinking of the sort of tasks or problems that are commonly discussed in general society
- Then try to evaluate and/or implement those those tasks
- I'm again not really sure how one would evaluate those things
- I guess one could at this point think about things like how many beings the future might contain and whether nonhumans are sentient, and then, based on what one learns, adjust the promisingness of each task separately
- But it would in many cases seem more natural to adjust the value of all/most future-focused interventions together, and of all/most animal-focused interventions together, etc.
All that said, as noted above, I don't think cause areas" should be the only unit or angle of analysis; it would also be useful to think about things like intervention areas, as well as what fields one has or wants to develop expertise in and what specific tasks that expertise is relevant to.
comment by EdoArad (edoarad) ·
2021-01-26T10:32:00.053Z · EA(p) · GW(p)
This seems to be true if it is possible to gradually grow within a cause area, or if different tasks within a promising cause area are generally good. This might lead to a good working definition of cause areas
comment by MichaelA ·
2021-01-26T11:02:40.886Z · EA(p) · GW(p)
I'm not sure I understand. I don't think what I said above requires that it be the case that "[most or all] different tasks within a promising cause area are generally good" (it sounds like you were implying "most or all"?). I think it just requires that the mean prioritisation-worthiness of tasks in some cause, or the prioritisation-worthiness of the identifiable positive outliers among tasks in some cause, are substantially better than the equivalent things for another cause area.
I think that phrasing is somewhat tortured, sorry. What I'm picturing in my head is bell curves that overlap, but one of which has a hump notably further to the right, or one of which has a tail that extends further. (Though I'm not claiming bell curves are actually the appropriate distribution; that's more like a metaphor.)
E.g., I think that one will do more good if one narrows one's search to "longtermist interventions" rather than "either longtermist or present-day developed-world human interventions". And I more tentatively believe the same when it comes to longtermist vs global health & dev. But I think it's likely that some interventions one could come up with for longtermist purposes would be actively harmful, and that others would be worse than some unusually good present-day-developed-world human interventions.
comment by EdoArad (edoarad) ·
2021-01-26T11:45:13.455Z · EA(p) · GW(p)
Yea, sorry for trying to rush it and not being clear. The main point I took from what you said in the comment I replied to was something like "Early on in one's career, it is really useful to identify a cause area to work in and over time to filter the best tasks within that cause area". I think that it might be useful to understand better when that statement is true, and I gave two examples where it seems correct.
I think that there are two important cases where that is true:
- If the cause area is one where generally working toward it will improve understanding of the whole cause area and improve one's ability to identify and shift direction to the most promising tasks later on.
- For example, Animal Welfare might arguably not be such a cause because it is composed of at least three different clusters which might not intersect much in their related expertise and reasons for prioritization (alternative proteins, animal advocacy and wild animal welfare). However, these clusters might score well on that factor as sub-cause areas.
- If it is generally easy to find promising tasks within that cause area.
- Here I mostly agree with the overlapping bell curves picture, but want to explicitly point out that we are talking about task-prioritization done by novices.
comment by EdoArad (edoarad) ·
2021-01-26T11:47:50.687Z · EA(p) · GW(p)
A contrasting approach is to choose the next steps in a career based on opportunities rather than causes, as Shay wrote [EA · GW]:
Another important point that I wish to emphasize is that I was looking for promising options or opportunities, rather than promising cause areas. I believe that this methodology is much better suited when looking at the career options of a single person. That is because while some cause area might rank fairly low in general, specific options which might be a great fit for the person in question could be highly impactful (for example, climate change and healthcare [in the developed world] are considered very non-neglected in EA, while I believe that there are promising opportunities in both areas). That said, it surely is natural to look for specific options within a promising cause area.
comment by MichaelA ·
2021-01-26T05:33:44.084Z · EA(p) · GW(p)
As explained (EA Forum link [EA · GW]; HT Edo Arad) by Owen Cotton-Barratt back in 2014, there are at least two meanings of "cause area". My impression is that since then, effective altruists have not really distinguished between these different meanings, which suggests to me that some combination of the following things are happening: (1) the distinction isn't too important in practice; (2) people are using "cause area" as a shorthand for something like "the established cause areas in effective altruism, plus some extra hard-to-specify stuff"; (3) people are confused about what a "cause area" even is, but lack the metacognitive abilities to notice this.
As noted above, personally, I usually find it most useful to think about cause areas in terms of a few broad cause areas which describe what class of beneficiaries one is aiming to help.
I think it'd be useful to also "revive" Owen's suggested term/concept of "An intervention area, i.e. a cluster of interventions which are related and share some characteristics", as clearly distinguished from a cause area.
E.g., I think it'd be useful to be able to say something like "Political advocacy is an intervention area that could be useful for a range of cause areas, such as animal welfare and longtermism. It might be valuable for some EAs to specialise in political advocacy in a relatively cause-neutral way, lending their expertise to various different EA-aligned efforts." (I've said similar things before, but it will probably be easier now that I have the term "intervention area" in mind.)
comment by EdoArad (edoarad) ·
2021-01-26T10:28:49.737Z · EA(p) · GW(p)
I really agree with this kind of distinction. It seems to me that there are several different kinds of properties by which to cluster interventions, including:
- Type of work done (say, Political Advocacy)
- Instrumental subgoals (say, Agriculture R&D (which could include supporting work, not just research)). (I'm not sure if it's reasonable to separate these from cause areas as goals)
- Epistemic beliefs (say, interventions supported by RCTs for GH&D)
(It seems harder than I thought to think about different ways to cluster. Absent of contrary arguments, I might purpose defining intervention areas as the type of work done)
comment by MichaelA ·
2021-01-26T05:44:29.429Z · EA(p) · GW(p)
In practice, Open Philanthropy Project (which is apparently doing cause prioritization) has fixed a list of cause areas, and is prioritizing among much more specific opportunities within those cause areas. (I'm actually less sure about this as of 2021, since Open Phil seems to have made at least one recent hire specifically for cause prioritization.)
Open Phil definitely does have a list of cause areas, and definitely does spend a lot of their effort prioritising among much more specific opportunities within those cause areas.
But I think they also spend substantial effort deciding how much resources to allocate to each of those broad cause areas (and not just with the 2021 hire(s)). Specifically, I think their worldview investigations are, to a substantial extent, intended to help with between-cause prioritisation. (Though it seems like they'd each also help with within-cause decision-making, e.g. how much to prioritise AI risk relative to other longtermist focuses and precisely how best to reduce AI risk.)
answer by Jason Schukraft
) · GW
A lot depends on what constitutes a cause area and what counts as analysis. My own rough and tentative view is that at some level of generality (which could plausibly be called "cause area"), we can use heuristics to compare broad categories of interventions. But in terms of actual rigorous analysis, cause area is certainly not the right unit, and, furthermore, as a matter of empirical fact, there aren't really any research organizations (including Rethink Priorities, where I work) that take cause area to be the appropriate unit of analysis.
Very curious to hear the thoughts of others, as I think this is a super important question!
comment by MichaelA ·
2021-01-26T06:02:20.957Z · EA(p) · GW(p)
I agree with your first two sentences. I feel unsure precisely what you mean by the sentence after that.
E.g., are you saying that no research organisations are spending resources trying to help people prioritise between different broad cause areas (e.g., longtermism vs animal welfare vs global health & development)? Or just that there's no research org solely/primarily focused on that?
My impression is that:
- There were multiple orgs that were primarily focused on between-cause prioritisation research in the past
- But most/all have now decided on one or more cause areas as their current main focus(es) for now, and so now spend more of their effort on within-cause-area work
- But many still do substantial amounts of work that's focused on or very relevant to between-cause prioritisation, and may do more of that again later. E.g.:
- Open Phil do worldview investigations
- 80,000 Hours continue to put some hours (e.g. [EA · GW]) into non-longtermist issues even if primarily longtermist issues are definitely their main focus
- GPI are currently focused mostly on global priorities research that's relevant to longtermism. But much of that is directly about how much to prioritise longtermism in the first place (partly to make a better case for longtermism, but I think also partly just because they're genuinely unsure on that). And I imagine much of their work is also relevant to prioritising between other cause areas, and that they may diversify their focuses more in future.
- Though I don't actually know a huge amount about GPI's work
- And there is also a bunch of non-research effort aimed at helping individuals think about which broad causes they want to/should focus on
answer by MichaelA
) · GW
I just stumbled upon this definition of a "cause" from GiveWell in 2013:
we’ve since moved to the cause as our fundamental unit of analysis. We’d roughly define a “cause” as “a particular set of problems, or opportunities, such that the people and organizations working on them are likely to interact with each other, and such that evaluating many of these people and organizations requires knowledge of overlapping subjects.”
That definition seems useful to me, though of course many other definitions are possible too.
Where I found that was a link from an 80,000 Hours post from 2013 on Why pick a cause?, in which they discuss 4 key reasons:
- Picking a cause is one of the best things you can do to increase your impact.
- We think picking a cause provides you with a useful level of direction in planning your next steps, which is neither too narrow nor too broad.
- Picking a cause seems to be a useful way to narrow down careers based on personal factors and deeply held value judgements.
- Having a cause can be motivating.
So that post seems relevant here.
(I think this largely repeats the sort of points made in other answers/comments, but I felt I might as well share these links and quotes anyway.)
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comment by NunoSempere ·
2021-01-26T15:50:17.582Z · EA(p) · GW(p)
So for me, the motivation for categorizing altruistic projects into buckets (e.g., classifications of philanthropy) is to notice the opportunities, the gaps, the conceptual holes, the missing buckets. Some examples:
- If you divide undertakings according to their beneficiaries and you have a good enough list of beneficiaries, you can notice which beneficiaries nobody is trying to help. For example, you might study invertebrate welfare, wild animal welfare, or something more exotic, such as suffering in fundamental physics.
- If you have a list of tools, you can notice which tools aren't being applied to which problems, or you can explicitly consider which tool-problem pairings are most promising. For example, ruthlessness isn't often combined with altruism.
- If you have a list of geographic locations, you can notice which ones seem more or less promising.
- If you classify projects according to their level of specificity, you can notice that there aren't many people doing high level strategic work, or, conversely, that there are too many strategists and that there aren't many people making progress on the specifics.
More generally, if you have an organizing principle, you can optimize across that organizing principle. So here in order to be useful, a division of cause areas by some principle doesn't have to be exhaustive, or even good in absolute terms, it just has to allow you to notice an axis of optimization. In practice, I'd also tend to think that having several incomplete categorization schemes among many axis is more useful than having one very complete categorization scheme among one axis.