This is the story of how I came to see Wild Animal Welfare (WAW) as a less promising cause than I did initially. I summarise three articles I wrote on WAW: ‘Why it’s difficult to find cost-effective WAW interventions we could do now’, ‘Lobbying governments to improve WAW’, and ‘WAW in the far future’. I then draw some more general conclusions. The articles assume some familiarity with WAW ideas. See here or here for an intro to WAW ideas.
My initial opinion
My first exposure to EA was reading Brian Tomasik’s articles about WAW. I couldn’t believe that despite constantly watching nature documentaries, I had never realized that all this natural suffering is a problem we could try solving. When I became familiar with other EA ideas, I still saw WAW as by far the most promising non-longtermist cause. I thought that EA individuals and organizations continued to focus most of the funding and work on farmed animals because of the status quo bias, risk-aversion, failure to appreciate the scale of WAW issues, misconceptions about WAW, and because they didn’t care about small animals despite evidence that they could be sentient.
There seem to be no cost-effective interventions to pursue now
In 2021, I was given the task of finding a cost-effective WAW intervention that could be pursued in the next few years. I was surprised by how difficult it was to come up with promising WAW interventions. Also, most ideas were very difficult to evaluate and their impacts were highly uncertain. To my surprise, most WAW researchers that I talked to agreed that we’re unlikely to find WAW interventions that could be as cost-effective as farmed animal welfare interventions within the next few years. It’s just much easier to change conditions and observe consequences for farmed animals because their genetics and environment are controlled by humans. I ended up spending most of my time evaluating interventions to reduce aquatic noise. While I think this is promising compared to other WAW interventions I considered, there are quite many farmed animal interventions that I would prioritize over reducing aquatic noise. I still think there is about a 20% chance that someone will find a direct WAW intervention in the next ten years that is more promising than the marginal farmed animal welfare intervention at the current funding level.
I discuss direct short-term WAW interventions in more detail here.
Some WAW advocates promote research on WAW in academia. For some of them, their aim is twofold: to identify effective interventions and establish WAW as a legitimate field of study. The hope is that by gaining greater legitimacy, WAW advocates can influence government policy. For example, governments could control wild populations more humanely, vaccinate animals against some diseases, and eradicate some parasites.
I am somewhat skeptical of this because:
- The argument for the importance of WAW rests on the enormous numbers of small wild animals. It’s difficult to imagine politicians and voters wanting to spend taxpayer money on improving wild fish or insect welfare, especially in a scope-sensitive way. But it could have been similarly difficult to imagine governments funding species conservation efforts until it happened.
- The consequences on the welfare of all affected wild animals seem nearly impossible to determine, even with a lot of research. Also, research in one ecosystem might not generalize to other ecosystems.
- However, this is the same as the concern of cluelessness that applies to all causes. That is, all interventions have complicated indirect effects that are impossible to predict. To me, cluelessness seems a bigger problem in WAW because first-order effects are usually dwarfed by second and third-order effects. For example, vaccinations may increase the population of that species, which could be bad if their lives are still full of suffering. Also, when the population of one species changes, it changes populations of other species too. But overall, I’m confused about cluelessness.
- Even if we determine consequences, people with different moral views might disagree on which consequences they prefer. For example, people may disagree on how to weigh the welfare of different animal species, happiness versus suffering, short and intense suffering versus chronic but less intense suffering, etc. This may eventually divide the WAW movement into many camps and hurt overall efforts.
See here for further discussion of the goals of lobbying governments to improve WAW, and obstacles to doing this.
Others have argued that what matters most in WAW is moral circle expansion and the effect we may have on the far future. But what exactly do we want to achieve in the far future with our current WAW work? In this article, I listed all the far-future scenarios where WAW seemed very important. The most important ones included scenarios where wildlife is spread beyond Earth. For example, we might develop an aligned transformative AI and the humans in charge might want to colonize space with biological human-like beings and animals, rather than machines. In that case, we could end up with quadrillions of animals suffering on billions of planets for billions of years. Compared to that, WAW interventions on Earth seem much less important.
However, to me, WAW doesn’t seem to be the most important thing for the far future - not even close. Digital minds could be much more efficient, thrive in environments where biological beings can’t, utilize more resources, and seem more likely to exist in huge numbers. Hence, some other longtermist work seems much more promising to me than longtermist animal welfare work.
If you think that the future is likely to be good, then I think that reducing x-risks is much much more promising. If you are a negative utilitarian (i.e., you only care about reducing suffering) or you are pessimistic about the future, you may want to prioritize work that aims to reduce the potential suffering of future digital minds instead (for example, the work of organizations like The Center on Long-term Risk). The tractability of trying to reduce digital mind suffering might be even lower than for longtermist animal welfare work, but the scale is much much higher. I think that there may be some worthwhile things to do in the intersection of longtermism and animal welfare but I don't think it that it should become a major focus for EA.
I discuss WAW and the far future in more detail here.
After looking into these topics, I now tentatively think that WAW is not a very promising EA cause because:
- In the short-term (the next ten years), WAW interventions we could pursue to help wild animals now seem less cost-effective than farmed animal interventions.
- In the medium-term (10-300 years), trying to influence governments to do WAW work seems similarly speculative to other longtermist work but far less important.
- In the long-term, WAW seems important but not nearly as important as preventing x-risks and perhaps some other work.
All that said, I’m unsure how seriously my opinions should be taken because:
- I don’t have an ecology/biology/conservation background to competently evaluate direct short-term WAW interventions,
- I don’t know enough about the history of social movements to evaluate how likely WAW is to succeed as a social movement, and
- I’m not very knowledgeable about longtermism.
Hence, I see my articles on WAW as the start of a conversation, not the end of it.
Despite my concerns, if I was in charge of all EA funding, I still wouldn’t set WAW funding to zero. Since it’s very difficult to predict which interventions will be important in the future, I think it makes sense to try many different approaches. I still believe that WAW is promising enough to do some further research and movement building. For example, even though I think that corporate farmed animal welfare campaigns are very cost-effective, I would not choose to drop all WAW funding in order to fund even more corporate campaigns, because WAW work could open an entirely new world of possibilities. We won't know what's there unless we try.
However, I wouldn’t spend much more money on WAW than EA is currently spending either. My subjective probability that the WAW movement will take off with $8 million per year of funding is not that much higher than the probability that it will take off with $2 million per year of funding, as the movement’s success probably mostly depends on factors other than funding. But with $2 million, the probability would be much higher than with $0 (I’m using somewhat random numbers here to make the point). And ideally, the money that we do spend on WAW would be used to fund people with different visions about WAW to try multiple different approaches so that we could see which approaches work best. I see some of this happening now, so I mostly support the status quo. Of course, my opinion on how much funding WAW should receive might change upon seeing concrete funding proposals.
[EDIT 2023-02-21: I criticized the version of the WAW movement I saw being pursued by organizations. To my knowledge, no organization currently works on WAW by trying to help microorganisms, or decrease wild animal populations (which perhaps could be done in relatively uncontraversial ways). I simply don’t have an opinion about a WAW movement that would focus on such things. There were some restrictions on the kinds of short-term interventions I could recommend in my intervention search. Interventions that would help microbes or help wild animals by reducing their populations simply didn’t qualify. Thank you to the commenters who made me realize this.]
Opinions expressed here are solely my own. I’m not currently employed by any organization.