Wild animal suffering is vast, neglected, and morally urgent. I’m strongly in favour of building a field that can eventually deliver safe, scalable welfare improvements for free-living animals. I also recognise that this area is technically complex and requires foundational research. But after reading WAI’s latest annual report, I simply have to ask:
When does any of this work actually reduce wild animal suffering?
WAI themselves say that ‘it’s reasonable to ask whether this will all be worth it’ on p. 28 of their most recent annual report. What then follows is an illustrative case study regarding rabies vaccination, with figures they describe as ‘back of the envelope’ and ‘intentionally crude.’
After 4-5 years and several millions in funding, I can’t find evidence in this report of an intervention, policy change, or measurable welfare improvement driven by WAI’s research. What’s more concerning is that the report doesn’t spell out a concrete timeline or milestones for when their research is expected to translate into specific welfare interventions or policy changes. Beyond vague phrases like ‘interventions relatively soon’ and a five-year plan to build presence in ecology, there’s no clear indication of when wild animals might benefit.
In other cause areas, research-first orgs (Rethink Priorities, HLI, etc.) publish pathways to impact, or at least some projections for when research might translate into tangible change. Without something similar, donors and talent can’t tell whether WAI is progressing or stuck in perpetual research.
So here are the questions I’d like to see clear answers to:
- When does WAI expect to produce its first real-world intervention or policy shift e.g. is there anything concrete expected this decade?
- What conditions would trigger a move from foundational research to applied work?
- What would indicate that the current strategy isn’t working and needs revision?
This isn’t a critique of WAI’s team - they seem genuinely thoughtful and mission-driven. It is a call for strategic clarity in a field with limited funding. I fully understand WAI’s explicit positioning as a research/field-building org; but I don’t think resources should continue to be deployed indefinitely without clearer checkpoints for when wild animals stand to benefit.
P.S. To shift gears for a moment: if it were up to me, I’d keep WAI primarily a research organisation; but I’d add a small, focused campaigning arm to push for welfare improvements informed by that research. That would give the field both the long-term, speculative impact and a credible path to near-term wins. Donors, policymakers, and talent all respond better when there’s something concrete to rally around. The annual report notes that ‘the historic neglectedness of this issue means that there are probably some relatively easy wins available.’ If WAI has identified even one or two of those over the past 4–5 years, why not move one forward and show proof of concept?
[2 of 6] Why hasn’t WAI implemented interventions yet?
In short: Because that’s not what we’ve been trying to do.
If we had been spending the last six years trying to find interventions that could be implemented as soon as possible, and our progress to date is all we had to show for it, then that would be extremely disappointing. If that’s what we’d been aiming for and this is where we landed, then I think it’d be fair to say we failed — or at the very least, we definitely shouldn’t be an ACE-recommended charity.
What we have been doing instead is pursuing a strategy that is entirely focused on building wild animal welfare science up into a self-sustaining academic field that is positioned to produce the research needed to reduce wild animal suffering as much as possible over the long run.
I’m glad you brought up Rethink Priorities and Happier Lives Institute, because I think the contrast between us is very illustrative. Like most EA research orgs, RP and HLI mostly conduct research with the aim of directly informing policymaking, philanthropy, or movement strategy. Although the particular topics they’re focusing on are highly neglected, those topics are often close enough to longstanding human concerns (e.g., public health, agricultural productivity) that they can build on the deep bodies of literature that have been developed by mature academic fields (e.g., development economics, human psychology, farm animal veterinary medicine).
Wild animal welfare science is at best several decades behind those fields. The problem is not that potential interventions haven’t been evaluated yet; it’s that we lack the basic scientific knowledge of how to evaluate most interventions. The few interventions we can evaluate with confidence are evaluable precisely because they have very limited impacts or only work under a narrow set of conditions.
That’s why we have optimized for field-building over intervention research: not because there are no interventions worth trying now, but because there’s a very low ceiling to how much impact you can have before you know how to measure welfare across different several classes and phyla, how to account for compensatory mortality, how to predict and monitor for effects on non-target species, etc.
Which is not to say we have done no research on interventions. Rather, we have chosen to research interventions insofar as we think it will contribute to field growth, such as by attracting interest and funding, providing opportunities to refine research methodologies, building bridges with relevant research communities, or simply serving as a proof of concept for the field.
I explicitly acknowledged your stated strategy and the need for foundational research. My question is when you expect that strategy to translate into real-world impact.
To move this forward, let’s try to crystallise what you’ve said:
1. What exactly counts as a self-sustaining academic field for wild animal welfare?
Is that defined by number of labs? Funding sources? Course offerings? Publication volume? ‘Self-sustaining’ risks becoming an unending horizon.
2. What does ‘the long run’ mean in practice?
A strategy without a time-bound target is very difficult to evaluate. Is the honest answer simply ‘as long as it takes’? As long as people are willing to fund it?
3. How much funding do you estimate is required to reach this self-sustaining point?
If the answer is ‘we don’t know’, that’s fine - but then we need some proxy indicators or budget ranges that would count as reasonable expectations.
Is the reality that donors are effectively funding an open-ended research project with no agreed stopping rule? Your answers make it hard not to reach that conclusion.
I'm not trying to exhaust you with relentless questions. I'm trying to separate the wheat from the chaff in what you've said. Long replies run the risk of diverting away from the central thrust of discussion.
[3 of 6] “When does WAI expect to produce its first real-world intervention or policy shift e.g. is there anything concrete expected this decade?”
Mandatory annoying disclaimer: For the reasons discussed in my preceding comment, I don’t think “time till first intervention implementation” is a useful proxy for the pace of field growth or the fidelity of its trajectory.
But to answer your question:
First past the post: Backyard bird habitat improvements in 1-2 years
WAI funded Ross MacLeod and colleagues to validate the use of eye temperature (assessed via thermal imaging) as an indicator of the welfare of several common bird species. If they find the metric to be usable as hypothesized, they can draw on over ten years of data they’ve collected from 54 backyard-like sites constructed to manipulate variables like bird feeder location, fencing presence/absence, and hedge species. If they find significant differences, Ross plans to use his longstanding relationships with the RSPCA and other UK bird groups to disseminate the first ever guidance on how bird lovers can set up their gardens to be more subjectively enjoyable for the birds that visit them.
Clearly this isn’t the most pressing issue facing wild animals, but happens to be on track to be the first of many cases where WAI-funded research identifies ways people can improve wild animal welfare by making simple changes to existing activities.
First high-confidence scalable intervention: Rodent fertility control in 4-7 years
Replacing anticoagulant rodenticides with oral contraceptives would remove a widespread source of intense, prolonged suffering. Because this would be modifying existing population management practices rather than changing an ecosystem in a novel way, fertility control offers an unusually convenient opportunity to reduce the suffering of a target population with minimal likelihood of affecting non-target populations.
Unfortunately, existing products have attracted more hype than the research supports, which has led to repeated failures of pilot projects launched by groups unaware of this track record.But because these compounds work in lab settings, there is strong reason to believe that an effective rodent contraceptive product can be developed (or that existing products could be made effective by following different application methodologies).
WAI has partnered with Conservation X Labs and the Botstiber Institute for Wildlife Fertility Control to outline a process for running a research competition that would incentivize private R&D labs to close crucial knowledge gaps and develop a demonstrably effective product. If funding allows, we’ll launch this process in summer 2026. It will take at least a year or two to run the research competition, and likely several more years to get a new product to market.
Once an effective solution is commercially available, it can be applied at larger and larger scales as it is adopted across more cities, farms, factories, and conservation efforts (invasive rodents are a major threat to rare species on remote islands).
Thanks for laying these out. I have to be honest: I don’t think these examples justify the current scale of investment.
A backyard bird-feeder optimisation study isn’t remotely proportional to the millions deployed so far, nor to the moral stakes that originally motivated WAI’s existence.
The rodent fertility control pathway sounds more promising, but again: a best-case 4–7 year pathway if funding materialises, if the competition succeeds, and if a viable product emerges.
If these are the strongest examples of expected real-world impact this decade, then that reinforces my original concern: the current spend-to-impact ratio looks extremely low, and the strategic timeline still feels unanchored.
[6 of 6] "What would make you know it’s not working?"
There are three levels at which you might answer this question:
(1) How would you know if field-building was the wrong strategy?
(2) How would you know if WAI's efforts weren't on track to succeed at field-building?
(3) How would you know if the field wasn't on track to lead to real change for animals?
Thanks for the clarifying comment, Cam!
Not very relatedly, in terms of cause prioritisation, I wonder whether it makes sense to prioritise building capacity for increasing digital welfare or that of soil animals. Do you have any thoughts on this? I estimate changing, not (robustly) increasing, the welfare of soil animals will remain more cost-effective than changing digital welfare for at least the next few decades.
Do you have any suggestions for analyses I could do to inform this?
[4 of 6] "What conditions would trigger a move from foundational research to applied work?"
I really do like arbitrary binaries for things that obviously aren't that simple ("all models are wrong, but some are useful"!), but in this particular case I think the binary might actually be too reductive to be useful. Still, I'll attempt to give a direct answer once I've done some quibbling.
First of all, applied work is already happening. There are many things people are doing to wild animals (typically for anthropocentric or biodiversity conservation reasons) that seem quite plausibly helpful for welfare (e.g., continuing to reduce the range of the New World screwworm). The difficulty is in determining whether these these interventions have net-positive effects once indirect effects on non-target species are accounted for. However, that doesn't mean we shouldn't do anything for wild animals until we're absolutely certain about the nature of the impact we're having. After all, everything that changes human or animal populations (e.g., distributing anti-malarial bednets, reducing factory farming) also has indirect effects on wild animals. So I think it's best to think of applied work not as something that will suddenly become possible, but rather something we'll gradually be able to do more strategically, confidently, and cost-effectively as science progresses.
Secondly, the need for foundational research won't necessarily go down for a long time, because answering some foundational questions will make it newly possible to address other foundational questions. Implementing progressively more ambitious interventions will certainly raise plenty of applied questions, which might themselves expose important gaps in foundational knowledge. While I realize this sounds like the classic researcher whose head is so far up their own ass the only words they can still get out are "more research is needed!", my thinking on this is actually more informed by my experience as an animal activist and what I've read about the history of the movement. As its focus shifted from pets to lab animals to farmed vertebrates to farmed invertebrates, the animal advocacy movement has repeatedly needed to consult more areas of science to inform its goals and tactics. I don't have a good sense of how often that raised truly foundational scientific questions, but at least right now the movement is greatly constrained by the lack of basic scientific (and even philosophical!) understanding of the nature of sentience, which seems extremely important to determining which invertebrates fall within the moral circle.
I'm not saying there's an infinite need for more research. Rather, I think we should acknowledge that research is likely to be a core function of the wild animal advocacy for the foreseeable future, and we shouldn't expect the need for foundational research to consistently go down as the opportunities for applied work increase.
For Wild Animal Initiative's part, we plan to continue pursuing both basic and applied research for the foreseeable future, and we hope the amount of resources devoted to that will continue to increase in absolute terms. In relative terms, we hope the proportion of the movement's resources spent on research generally declines over time, as research reveals more and more pathways for applied work. But we think most of that work should be done by other organizations. As a scientific organization that isn't part of an academic institution, it's essential for us to maintain credible in the eyes of scientists, and tying ourselves to particular campaigns or policies increases the risk that we will be seen as putting "an agenda" ahead of the pursuit of the truth. That risk could be mitigated, so we continue to explore strategies that involve us branching out. Our rule of thumb for now is we want to be involved in applied work when we can clearly position ourselves as scientific advisors to a project others are leading, as we're currently doing in our collaborations with Conservation X Labs (which will lead the rodent fertility control open innovation challenge, funding permitting) and the NYU WILD Lab (which works at the intersection of wild animal welfare science and municipal policymaking).
Finally, my attempt to answer your question directly: Given the aforebabbledabout fuzziness of the boundary between foundational and applied work, perhaps it would be useful to reformulate the question along these lines: "Under what conditions would we want the movement to be applying the majority of its resources to choosing and implementing interventions, rather than doing research that isn't directly targeted at specific interventions?"
Perhaps those conditions would include:
[5 of 🧵] Re adding a campaigning arm:
I don't want to steal anyone's thunder, but for now I'll just say:
I can barely contain myself. :)
If useful for calibrating, when we launched WAI, I expected it to take 50+ years to feel excited about any large-scale interventions. That level of investment at current wild animal welfare spending levels seems very worth it given the scale of the the issues at stake — at current levels, it would cost less over 50 years than is spent on farmed animal welfare in a single year, and farmed animal welfare is a much smaller problem by many orders of magnitude.
But my timelines for good WAW interventions are now much shorter - on the order of a few years (so I guess making a correct original prediction at more like 10-15 years). That's partially due to WAI having a lot of success in building a pipeline for research, but also due to me thinking that non-target effects are less important to understand perfectly than I used to and due to me no longer thinking other animal interventions (with a few very notable exceptions) are particularly cost-effective, such that I think the kinds of interventions on the table in the near future for wild animals look much more promising.
Hi Abraham, thanks for your comment. A quick clarifying question: when you say timelines have gone from 50+ years to a few years, what interventions are you referring to?
Cameron mentioned examples such as bird-feeder design changes and rodent fertility control. Are those the interventions you had in mind when saying that the field is much closer to actionable work?
It would be helpful to understand what fits the updated timeline, and how this aligns with Cameron's explanation.
A non-exhaustive list of things that seem like plausible candidates from a scale perspective, but are at varying points in the quality of research (and many are probably not near the certainty level we would need on the overall sign, but could be fairly easily, at least for target effects), and a rough guess at the scale of the number of animals that could be impacted by target effects:
All of these seem feasible in the nearer future, but still are minor compared to the scale of the bigger problems in the space, which I think academic field building is fundamental to address. If I could choose only one, I'd choose doing further academic field building over implementing any of these (though luckily we don't have to choose between them).
(also, to be clear, WAI's views might be very different than my own - just trying to give a flavor of what kind of timelines I was thinking about when setting up WAI).
Thanks for laying those out. I’d agree that if even one were executed at scale it could be a major win for animals. However, WAI doesn’t appear to have a pathway for turning any of those into reality. The reason for this seems to be ‘we’re not certain enough yet’, but there isn’t a defined threshold for what ‘certain enough’ means.
Field-building has value, but it shouldn’t be the default answer indefinitely, especially when the projected timelines for impact seem to shift so dramatically (suggesting that the original thesis was off, albeit in a direction that’s good for animals). There also isn’t a clearly defined threshold for how much field building is sufficient.
At some point, the movement ought to have clarity on when possible interventions graduate from speculative ideas to actionable programs.
Let’s see where things stand in a few years.
[1 of 6]
Hi Siobhan! Thanks so much for sharing your concerns and giving us a chance to explain our work!
I'm embarrassed to say I failed to find a brief way to answer your questions, so you'll have to forgive my lengthy staggered replies. I've posted them in separate comments to allow for discussion to proceed in different directions across separate threads.
Stream-of-consciousness meta commentary I jotted down before writing my actual replies:
Can I just say: Hell fuckin’ yeah, let’s fuckin’ go, I fuckin’ love EA. This is the noblest possible use of the EA Forum: Bluntly calling people on their shit in a way that is not just polite but also deeply compassionate and clearly in good faith. I’m just so glad that my life path took me into a community that works together with this particular cocktail of conflict and collaboration. I love you guys :’)
Hi Cameron, thank you for engaging in the spirit in which my post is intended. You could've just ghosted it and hoped nobody noticed. Really, I appreciate your time here.
Thanks Siobhan!
I'm looking forward to continuing the conversation soon, but unfortunately I had a medical emergency and I'm still not feeling myself, so it might be another day or two until I have the headspace to reply to your comments. Thanks for your patience.
CC @Vasco Grilo🔸
Of course, no pressure. I hope it's nothing permanent, and get well soon.
Thanks for the post, Siobhan! I strongly upvoted it, also because it resulted in insightful comments from Cameron Shorb.