Note: Before the launch of the Open Philanthropy Project Blog, this post appeared on the GiveWell Blog. Uses of “we” and “our” in the below post may refer to the Open Philanthropy Project or to GiveWell as an organization. Additional comments may be available at the original post.

We’ve completed a medium-depth writeup on geoengineering research - large-scale interventions in the climate to attempt to reduce climate change or its impacts - focusing on research around efforts to artificially cool the planet. This writeup outlines the basic case for why geoengineering research might be a promising cause for philanthropy, as well as listing all of the funded projects we know of in a spreadsheet. It is a medium-depth, rather than shallow-depth, investigation, in that it involved many conversations and represents our attempt to speak to a broad, representative set of relevant people (rather than the 1-3 conversations that typically constitute a shallow-depth investigation). With that said, it leaves many questions unanswered, and leaves us a fair distance from having a confident view on the value of philanthropic investment in geoengineering.

In this post, we first summarize why we’ve looked into geoengineering, what we’ve learned about it, and what we see as the pros and cons of geoengineering as a philanthropic cause. We then address a series of meta-questions: why are we pausing our investigation here? What would it look like to do a deeper investigation? What is a reasonable goal for a medium-depth investigation? Making progress on these sorts of questions is a key goal of our current ongoing research, which is why we’ve gone ahead with some medium-depth investigations of causes that we’ve had only very preliminary reasons to be interested in.

Why did we investigate geoengineering?
We’ve previously completed a shallow investigation of climate change, which concluded that (a) there is a substantial amount of giving around climate change mitigation; (b) one of the most concerning aspects of climate change is the uncertainty around forecasts of potential effects, which cannot rule out the possibility that climate change could be far more catastrophic than mainstream projections anticipate.

At the same time, we had read about the possibility of geoengineering: a broad term for large-scale efforts to modify the climate, which (a) was alleged to be overlooked by traditional environmental funders and nonprofits; (b) could be extremely risky but could also conceivably be our best option if facing a far-worse-than-anticipated catastrophe. As of the time when we completed our shallow investigation of climate change, geoengineering research was the most promising-seeming aspect of climate change philanthropy we had identified, based on the combination of having little attention from philanthropists and of having potentially crucial importance in the worst case. Because of this, and because climate change is one of the causes most widely held to be of paramount importance, we decided to put some further time into investigating geoengineering research as a philanthropic cause.

After a number of conversations with experts in the field, and attending a conference devoted to geoengineering research, we feel that our initial narrative of limited funding and potentially large importance continues to hold up. However, there are many questions that we would like to answer before committing funding to the field, and we expect that they will be fairly difficult and time-consuming to answer. We accordingly decided to pause and write up our current views.

What have we learned?
Details are at our writeup. In a nutshell:
  • We focused on a particular category of geoengineering, solar radiation management, that we perceive as riskier, potentially faster and cheaper (and thus more useful in a severe catastrophe), and less well-funded than the other major category (carbon dioxide removal).
  • It appears that this type of geoengineering could bring extreme risks, both environmental and political (through e.g. disputes over who has the right to intervene in the global environment). Funding research into it could conceivably do major harm by causing it to be perceived as a more viable option by policymakers.
  • At the same time, it is plausible that, in the event of a far-worse-than-projected climate-change-related catastrophe, this type of geoengineering could relatively quickly halt or reverse global warming. Better information about the costs, benefits, and best methods of implementation could therefore be highly valuable in such an event.
  • We haven’t found any funders - governmental or philanthropic - spending large amounts in this area now, and the field appears relatively small with relatively little in funding. (Our attempt to identify funded projects and funding sources around the world that explicitly include a significant solar geoengineering component came up with a total of about $11 million/year in funding, though we believe that figure is more likely than not to underestimate the total resources devoted to solar geoengineering research.)
  • There also doesn’t appear to be much in the way of “shovel-ready” funding opportunities, and it isn’t immediately clear how a funder would contribute to the field. Promoting more discussion of whether geoengineering research should be expanded - and how to handle the governance issues (e.g., who has the right to carry out experiments that may affect the global climate) - could be a better strategy than simply funding more research. A funder’s involvement in this area could be in the category of “field-building” - funding and organizing convenings and encouraging more people to enter the field - rather than supporting existing organizations.

Pros and cons of geoengineering research as a philanthropic cause
We see major reasons to be positive on the value of geoengineering as a philanthropic cause, and major reasons to be negative.


  • The relative lack of existing philanthropic (and governmental) funding is striking. When comparing geoengineering research to other causes we’ve done shallow investigations on (including those in progress), the total dollars in the area seem very low, and the dollars are spread out among an assortment of funders.
  • Climate change is one of the most compelling global catastrophic risks we’re aware of, and in the event that climate change is far more catastrophic than currently projected, it seems that having better information on geoengineering could make a crucial difference - whether that information enables and improves geoengineering (which could be the only viable option for mitigating global catastrophe) or whether it prevents geoengineering from being carried out (by strengthening the case that the costs outweigh the benefits).
  • As a more minor point, it isn’t necessarily the case that better information about geoengineering will be fully useless in a more “normal” (closer to mainstream projections) scenario. Studying the methods and consequences of intervening in the global climate could produce insights with a variety of applications.


  • The experts we spoke with were not uniformly encouraging about the value of getting involved in this space, and in some cases expressed ambivalence on the basis that increased attention for geoengineering could cause harm by (a) making risky geoengineering interventions more likely; (b) lowering the perceived importance of carbon emissions reduction. We’re extremely wary of getting involved in any cause in which some of the people with the most inside knowledge are ambivalent/less-than-enthusiastically-positive about seeing a new funder enter.
  • The case for geoengineering research being important hinges on a highly specific long-term set of conditions. It hinges on the idea that our involvement now would cause more progress on generating useful information than would be achieved otherwise over a very long time frame (a risky proposition since improved technological tools and greater attention to the issue in the future could swamp what can be accomplished in earlier years); that climate change presents enough of a problem in the fairly far future for geoengineering research to be relevant; and that the marginal “useful information generated” by philanthropy over the next few years turns out to be important for policymakers.

Why are we pausing our investigation here?
The general principle we’re trying to follow with investigations is, “Pause an investigation when the effort required to significantly improve our understanding is significantly beyond the effort we’ve put in so far.” For our shallow investigations, we generally talk to 1-3 people; for medium-depth investigation, we generally try to talk to enough people to create a preliminary landscape of the cause. In the case of geoengineering, the cost of achieving the latter relative to the former seemed relatively small, so we went ahead. But from here, substantially improving our understanding would likely have to mean gaining a deep understanding of the scientific and/or political issues, which could take months or even years, and the returns to a few more conversations seem unlikely to be high.

What would it look like to do a deeper investigation?
It seems to us that a funder in this area would have to make difficult judgment calls about controversial questions, such as whether the benefits of more discussion around geoengineering outweigh the costs. This is the sort of endeavor that we feel is likely to require true subject-matter expertise, and for that reason the next step in investigating geoengineering would likely to be to seek out a full-time employee to specialize in it, or to hire someone who already has considerable expertise. This is consistent with our strategy, described earlier this year, of focusing our efforts on finding causes to recommend developing philanthropic capacity in, rather than on finding projects to recommend funding directly.

We are currently experimenting with working with a consultant (who has a substantial relevant background) to make more progress on this cause.

What is a reasonable goal for a medium-depth investigation?
We’ve been eager to move forward with investigations of causes that seem unusually promising to us, even if they seem promising for highly intuitive and not very thoroughly researched reasons. This is because we are seeking to learn about what to expect from an investigation as much as we’re seeking to learn about the causes themselves.

In this case, we feel that coming to a bottom line on whether and how a philanthropist could accomplish good by supporting geoengineering-related activities would take a great deal more investigation - so much so that it likely requires at least one dedicated full-time person over an extended period of time. In other words, we don’t feel that a medium-depth investigation has been sufficient to identify or assess specific giving opportunities.

However, we think the medium-depth investigation has given us important information that will be useful in determining the value of a deeper (full-time-person) investigation. We’ve established a more confident view that geoengineering is in some sense a “neglected” area of philanthropy; we’ve established that funding it would likely require a “field building” type effort rather than simply supporting existing organizations that are already ready to scale; we’ve established that there is controversy within the field and that an investigation would have to be thorough and careful in order to reach a well-grounded bottom line on whether and how to get involved.

Armed with this level of information about many causes, a funder would be able to make much more informed decisions about which causes to make commitments to (whether in the form of hiring people to investigate them more deeply, or in the form of funding existing organizations, or both). This doesn’t mean that there would be any particular formula for making provably, or quantifiably, optimal decisions, but it does mean that such decisions would likely be more rational than the way most funders choose causes. That’s the goal of strategic cause selection.

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