Wild Animal Initiative: When does research become impact?

[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. 

[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).

[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?

• If AI changes the nature of research so much that academia becomes irrelevant.
  • This seems the most plausible way our field-building strategy could be wrong, but so far we haven't found a strategy that seems more robust to the huge uncertainties created by AI. If you have an idea for an alternative strategy that seems reasonably likely to be much more robust than field-building, please let us know, because this is an active area of strategic research for us.
• If someone finds a way to reduce suffering for ~trillions of wild animals that doesn't require more research/technology (either to implement or to evaluate), that can be shown with high confidence to be net-positive even after accounting for effects on non-target species, and that seems likely to shift social norms toward caring explicitly about wild animal welfare over the long run.
• If there's massive social change in favor of wild animal welfare -- something like the way pollution and habitat destruction rapidly became issues of wide concern in the US between 1962 (when Rachel Carson published Silent Spring) and 1970 (when Richard Nixon founded the Environmental Protection Agency and Gaylord Nelson organized the first Earth Day). If that happened, it would be reasonable to expect an academic field to emerge somewhat organically, the way conservation biology did in the 1980s.

(2) How would you know if WAI's efforts weren't on track to succeed at field-building?

• This is the failure mode we invest the most in monitoring. We're tracking a wide range of metrics related to field growth and indicators related to our causal impact. We're still building up that system (collecting historical data, deciding which metrics are most relevant, etc.), but we hope to have an easily shareable dashboard sometime early in 2026. For now, I suggest looking at the supporting documents in Animal Charity Evaluators' 2025 recommendation of WAI to get a more detailed look at how we approach monitoring and evaluation.

(3) How would you know if the field wasn't on track to lead to real change for animals?

• We think it this will be pretty hard to get data on before the field is more established (i.e., at least another 5 years), because as long as the community is still evolving, its present form isn't necessarily representative of its long-term state.
• For now, we're looking for positive indications that our priorities are increasingly represented within the field: valuing highly abundant populations/taxa, researching invertebrates, considering counterfactuals, being open to human interference in nature, accounting for the possibility of net-negative lives, etc.
• Negative signs might include indications that some sort of sub-optimal culture is dominating and self-perpetuating (particularly concerning if the culture represents a relatively small part of society at large, because that would suggest our field is actively selecting for it, rather than failing to filter it out). For example, wildlife management science was heavily populated by hunters and anglers until recently; veterinary medicine is primarily funded by animal ag interests and continues to have a strong pro-farming culture. (I don't know to what extent these particular trends in academic subcultures exist outside the US.)

[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:

• We have methods to empirically measure welfare within enough precision across a broad enough range of species that we can confidently make habitat-level land management decisions (i.e., is the total wellbeing of all the animals higher in cropland A or cropland B, forest C or forest D, cropland A or forest C, etc.). This isn't strictly necessary to take action, but it would open up such a huge category of tractable actions that applied work would likely be able to absorb more resources than foundational work.
• Within wild animal welfare science and adjacent academic communities, there is a common understanding of welfare as something that is distinct from biodiversity, naturalness, economic value, or other values traditionally pursued by conservationists and other land managers. This would represent a major milestone on the path to a society that understands and values wild animal welfare enough for welfare to be a common consideration in policy discussions (similar to how ideas like biodiversity, carbon sequestration, or environmental justice factor into policy discussions now: rarely the single highest priority, but widely understood and treated as good things to advance when possible). Again, this isn't necessary to take action, but the more widely welfare is understood and valued, the more likely it is that efforts to improve wild animal welfare will have positive long-term effects on social norms, which makes it more worthwhile to take action even if the short-term effects are uncertain. 

[5 of 🧵] Re adding a campaigning arm:

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.

I don't want to steal anyone's thunder, but for now I'll just say:

1. I totally agree the movement should have something like this (thought it would be most effective if separate from WAI).
2. There's some really exciting news coming on this front, which will likely be announced within the next week or two. Keep your eyes on the EA Forum!

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.

[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.

Thanks for the post, Siobhan! I strongly upvoted it, also because it resulted in insightful comments from Cameron Shorb.