The GiveWell Blog

Geoengineering research

[Added August 27, 2014: GiveWell Labs is now known as the Open Philanthropy Project.]

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.


  • Seth Baum on October 17, 2013 at 1:57 pm said:

    I might suggest thinking about the strategic significance of the in-field controversy. Should philanthropy seek to resolve the controversy? Should philanthropy only pursue projects that are not controversial? How questions like these are answered could heavily shape what projects philanthropists (or others) pursue. This is especially important for geoengineering because the controversies are, in my own observation, deep and potentially intractable. More specifically, they are often rooted in divergent world views and not in divergent reads of the science. (E.g., is geoengineering clever or hubristic?) A possible response is to pursue a sociology of geoengineering to inform paths forward. But if the controversy is of less strategic significance, then such an approach would be unnecessary.

  • Alexander on October 17, 2013 at 2:27 pm said:

    Seth – we agree that the internal controversies are significant, and it’s something we’ve thought about to some extent. We don’t have a fully developed theory of what the appropriate role for a philanthropist in this field would be, but as Holden wrote above, we think growing the field and the number of informed participants, without necessarily trying to dictate solutions, may be an important part of the story.

  • Russell Seitz on October 17, 2013 at 4:22 pm said:

    It would appear that in-depth analysis has been subordinated to the agenda summarized last week by w Secretary-General Angel Gurría of the Organization for Economic Co-operation and Development, who in a London address entitled The climate challenge: Achieving zero emissions declared:

    “Governments …If they are serious about climate change …can leave no stone unturned – all avenues to price carbon in a cost-effective way need to be explored and all conflicting policy signals eliminated.

    A critical element in this is… ensuring the right regulatory arrangements are in place “

    These are words calculated less to broaden the policy dialogue than terminate it.

  • J. S. Greenfield on October 17, 2013 at 7:41 pm said:

    While there’s no question that, at present, proposed geoengineering techniques to combat climate change carry huge risks, I have to agree with Seth that much of the opposition to geoengineering is less about the risks, than using the risks as a rationalization for a philosophical objection. There are many who philosophically reject geoengineering as a solution, because of what really seems to be an ascetic belief that it’s not the “right” way to solve the problem.

    If those objections were really about risk, given the great potential for such approaches, the objective reaction to the risks ought to be precisely to pursue research, in order to identify possible solutions with reduced risks.

    Holden, you talk about focusing on this area for the primary purpose of having potential solutions in case actual climate change turns out to be worse than mainstream projections. But to my view, we have no evidence of any successful implementation, or path to implementation, of solutions sufficient to address even the mainstream projections. And as some observers have noted, this class of problem (something slow moving, where the negative effects have significant uncertainty, and aren’t expected to occur for a long time — politically speaking) is one that humans have proven to be extremely bad at addressing. (That is, extremely good at kicking the can down the road.)

    So it seems to me that, in reality, geoengineering techniques may be important even if the maninstream projections are correct.

    In fact, given the relative speed with which geoengineering techniques could have impact (compared to the speed of impact of carbon emissions reductions), we could very easily end up in a situation where geoengineering techniques are the only viable solutions.

    That is, I don’t think there’s really a factual basis to believe that geoengineering research will undermine carbon reduction policy initiatives, because I don’t think there’s a factual basis for optimism that carbon reduction policies will ever be effectively adopted.

    To my view, the objective conclusion is that it’s essential to research geoengineering techniques in order to ensure that geoengineering solutions with lower risk are available as tools, vs. only having high-risk geoengineering solutions available.

  • Eric Durbrow on October 17, 2013 at 10:09 pm said:

    Can volunteers help Givewell in conducting a medium-depth investigation? E.g. interviewing by email, collecting information, very simple analysis?

  • Eric Durbrow on October 17, 2013 at 10:13 pm said:

    I was unable to find any consideration of marine cloud brightening in the spreadsheet or on this site. This seems among the least riskiest and most feasible of options and there seems to be two teams actively developing this. Did I miss it?

  • Colin Rust on October 20, 2013 at 8:11 pm said:

    In addition to mitigation and geoengineering, it seems to me that potentially a third broad class of interventions to deal with climate change is adaptation: what can we do to mitigate the effects of global warming? Has there been much philanthropic work on adaptation?


    On the issue of controversy and geoengineering: My sense is CDR is (quite reasonably) much less controversial than SRM (because of issues like ocean acidification and the risk of unforseen consequences). But of course the issue with CDR is will it work, at what scale and what speed which as I understand it is why you focussed on SRM; that sounds plausible to me (SRM sounds like it might be a better insurance policy to buy time in an extreme scenario).

  • Colin Rust on October 20, 2013 at 8:28 pm said:

    Just to be clear on the controversy point.

    There is definitely some controversy about CDR, but that’s (primarily) skepticism that it will be successful on a reasonable scale and, relatedly, that pursuing it might be a distraction from mitigation (which is basically starting from a view that it is unlikely to succeed).

    But with SRM, there is lots of controversy, partially about whether it could work on its own terms, but especially about how good a thing it would be even if it were successful.

  • Alexander on October 21, 2013 at 9:59 pm said:

    Thanks all for the comments.

    Eric – we mostly focused on stratospheric aerosols, rather than marine cloud brightening, though I believe some of the listed projects include an MCB component. As we write at our main geoengineering writeup: “We have not done any systematic comparison of the case for funding further research on SRM compared to further research on CDR, and we have looked at only a subset of all possible SRM approaches, for instance, not thoroughly investigating albedo modification or marine cloud brightening. We regard these as important questions for further investigation should we proceed further with this research.”

    Colin: we haven’t seen a systematic breakdown of philanthropic funding across mitigation and adaptation. Our anecdotal understanding is that philanthropic spending on mitigation is considerably larger than on adaptation, which is considerably larger than on geoengineering. The Rockefeller Foundation, for instance, has a program on climate resilience.

    I agree with your assessment that CDR is less controversial than SRM.

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