Why I'm focusing on invertebrate sentience

I wrote this post because I’m looking to get feedback on my plans, to describe a neglected research path to others, and to seek funding for continuing to research in this area. I don’t have a strong academic background in this area (I just have a philosophy BA) but I’ve been especially interested in the question for around six years now. I’ve now finished a contract with Rethink Priorities on invertebrate sentience. I’ve also spent around the last nine months studying it. If you’re interested in funding me or collaborating please get in touch! Use the term "sentience" synonymously with "phenomenal consciousness."

Doing research on invertebrate sentience would also tend to involve some research on vertebrate sentience because much of the literature of which criteria to use to assess sentience is done in the context of vertebrates. This would mean that invertebrate sentience research would also contribute to research on vertebrate sentience, though this would not be the priority.

I’m generally not talking about cephalopod sentience because cephalopods have a much stronger case for their sentience already, they are much less numerous than smaller invertebrates, and more people are already concerned for their welfare. My position on sentience is relatively similar to Luke Muehlhauser’s, as presented in his Report on Consciousness and Moral Patienthood. My approach is inspired by him.

In addition to the agent-neutral reasons I will present in this post about why we might want to focus more resources on invertebrate sentience, I think I have a strong comparative advantage in doing invertebrate sentience research compared to other things that we have strong reasons to focus on, like AI safety research.

Importance:

The two main ways that I see this research having an impact is by better informing us to make decisions about improving well-being and by functioning as a form of indirect advocacy. I think that it can help us better make decisions about current interventions (such as humane insecticides) as well as understand consciousness better so that we can create happy minds and not create suffering minds.

Though much research remains to be done on the question, humane insecticides seem to me to have a lot of potential as a robust way of reducing suffering now. The idea would be to try to get farmers to adopt insecticides that either killed more quickly than current insecticides, killed through a less painful mechanism, or perhaps did not kill nontarget species of insects.

Humane insecticides as an intervention seems to both have higher expected value and to depend on fewer ecological assumptions than other methods of helping wild animals. The sign of the intervention also does not depend on whether insects live net positive or negative lives. Research on invertebrate sentience is probably complementary to work on getting humane insecticides implemented.

One of the main ways research may also be able to help is as a form of indirect advocacy. I believe that society should be thinking a lot more about invertebrate sentience, and research can raise awareness about this issue. Research might be less directly persuasive then more direct forms of advocacy (because it is not optimized for that purpose), but I think that there is also less worry about backlash from it. It also seems to me like there needs to be a combination of advocacy and research to support that advocacy, or else the advocacy will not be well seen. One reason for this is that advocacy is more zero-sum than research because from the perspective of society advocacy shifts the distribution of the pie whereas research increases it. This more cooperative nature is another reason why research is important. In practice is probably a fine line between pure research and direct advocacy, but it is possible to strike different balances between them.

I also believe that invertebrate sentience research may be promising if you accept the overwhelming importance of the far future. This is because invertebrate sentience research may be applicable to the question of digital sentience. There may be many simple, potentially conscious, digital minds in the future, and understanding if they are conscious seems important so that we can avoid creating a lot of suffering and create a lot of happiness.

When I bring this up with EAs who are focused on AI safety, many of them suggest that we only need to get AI safety right and then the AI can solve the question of what consciousness is. This seems like a plausible response to me. However, there are some possible future scenarios where this might not be true. If we have to directly specify our values to a superintelligent AI, rather than it learning the value more indirectly, we might have to specify a definition of consciousness for it. It might also be good to have a failsafe mechanism that would prevent an AI from switching off before implementing any scenario that involved a lot of suffering, and to do this we might have to roughly understand in advance which beings are and are not conscious.

While some of these scenarios seem plausible to me, they are also somewhat specific scenarios that depend on certain assumptions about the importance of AI in the future and how the process of AI alignment might go. I think understanding digital sentience may be more robustly good than AI alignment research because in a greater variety of future worlds, understanding digital sentience will be important.

In my research I intend to focus somewhat on the question of digital sentience, but still focus mainly on invertebrate sentience even though I view the question of digital sentience as more important. This is because I view invertebrate sentience research as more robustly good, more tractable, less weird looking, and as also contributing significantly to our understanding of digital sentience. If we were closer to achieving digital sentience then I would focus more directly on that question.

I believe research on invertebrate sentience contributes to our understanding of digital sentience and vice versa. Indeed, all research on sentience is helpful for doing research on any other kind of sentience. For understanding the possibility of sentience in beings who are very different from us it is helpful to understand cases of sentience that are clearer to us, so that we can understand what we are looking for. Researching digital sentience (and the possible sentience of other entities such as plants or bacteria) can also give us perspective that helps with our understanding of invertebrate sentience, but for now I think researching invertebrate sentience is more promising.

Neglectedness:

Invertebrate sentience research may be very neglected. With rare exceptions, most people do not care at all about invertebrate sentience. This lack of caring may be largely due to factors that are not morally defensible, such as the fact that invertebrates look very different from us or are much smaller than us.

Invertebrate sentience research is somewhat less neglected than general efforts to help invertebrates. Some relevant research gets done out of intellectual curiosity, and quite a bit more research than that gets done because it helps humans in some way. There is a much smaller amount of research done directly on the question of invertebrate sentience. I tend to think that invertebrate sentience research is more important than current efforts to help invertebrates because invertebrate sentience research may shape the far future more than interventions to help invertebrates now.

Invertebrate sentience research lies at the intersection between biology, philosophy, neuroscience, and computer science to some extent. This tends to mean that there are fewer experts in this area than one might expect. Many invertebrate biologists who might otherwise have a lot to contribute in the area are not philosophically inclined, and have not thought about the ethical implications of their knowledge, and so become confused about the question of insect sentience.

Tractability:

I don’t believe that research on invertebrate sentience is very tractable. This is because consciousness is a thorny issue. Some authors such as Daniel Dennett have claimed to explain consciousness, but they haven’t offered us plausible criteria for determining that an entity is or is not conscious. And this is what we need to find. However, I do think that due to its neglectedness, there is some room for making more progress on the question than might be expected given its intractability.

Luke Muehlhauser claims (and I agree) that we would be hard-pressed to assign a very high or very low probability to invertebrate sentience. This would suggest that there is a ceiling on how useful further research may be on this question. Muehlhauser also mentions (and I agree) that adjusting the probabilities you assign the sentience of different entities does not affect the expected value dramatically. For example, the difference between assigning a 5% probability and a 50% probability is epistemically vast but arguably practically insignificant. It merely affects the amount of expected value represented by invertebrates by one order of magnitude. There are very roughly 10^18 insects in the world, and this number is still multiple orders of magnitude higher than the number of vertebrate animals.

This would suggest that working on invertebrate sentience is not important. However, there are some good arguments that talking about degree of sentience makes sense, and our best assessment of the degree of sentience of an entity is something that more plausibly can be shifted multiple orders of magnitude through research into the question.

It also seems plausible that many of the same arguments about why an invertebrate species might be more likely to be sentient also apply as arguments about why that species might have a higher degree of sentient (if they are sentient at all) . This is because most of the best arguments why an invertebrate species might be more likely to be sentient points to a similarity related to sentience in us between our mind and theirs. Similarities between our minds and theirs are also evidence of similar degrees of sentience. This means that we may not have to prioritize much between these two approaches. This has been my impression so far, but I imagine future research might indicate to me more ways that would provide evidence for one of these without providing evidence for the other.

Most people do not make an expected value calculation when it comes to these questions, and so doing research on the likelihood of invertebrate sentience can still be useful to update and persuade them. In my experience, most people typically roughly treat the question of invertebrate sentience as being either yes (100%) or no (0%).

What my next steps would be:

I particularly want to do research into degree of sentience and write about that. I plan to write shorter blog posts as I go because it is easy enough to do, helps me consolidate knowledge, and gives me a faster feedback loop. I will also try to work on some longer, more polished, documents. I will in all likelihood continue to update the table of potential consciousness indicating features that will be published with the report on invertebrate consciousness I worked on with Rethink Priorities.