Speedrun: Develop an affordable super PPE
This post is a shallow investigation of the intervention of developing better, cheaper, and easier-to-use personal protective equipment (PPE).
The post is part of a sequence of speedrun research projects by Rethink Priorities’ general longtermism team. I recommend you begin by reading the introductory post in the sequence if you haven’t already for information about the context of this post.
A quick context tl;dr:
The aim of this investigation was to help our team decide if we should take steps towards incubating an organization focusing on this project. Keep in mind that some of the conclusions take into account considerations (such as our team’s comparative advantage) that may not be relevant to the reader.
The investigation was intended to be very early-stage and prioritize speed over rigor. We would have conducted a more in-depth investigation before launching any projects in this space (and recommend that others do the same).
This post was written in early fall 2022; the funding situation has changed significantly since then, but the investigation has not been updated to reflect this. As such, the funding bar alluded to in the post is probably outdated. My quick guess is that this does not significantly affect the bottom line in this case; at least I think this project is still likely to rank relatively highly among biosecurity-related projects.
I spent ~15 hours researching and writing this speedrun. I have no other experience with biosecurity research and I don’t have a natural science background. So: I’m a junior generalist who has thought about this for a couple of work days, and as a result, this post should be considered very preliminary and likely to contain mistakes and bad takes. My goal in publishing this regardless is that it may be useful as (a) a primer gathering useful information in one place, and (b) an example of the kind of research done by junior generalists.
I’m generally optimistic about work being done to develop better PPE: I think it’s ~60% likely to be in the top 20 of the project ideas on our current list excluding considerations about Rethink Priorities’s fit for supporting a project like this.
My analysis of the merits of this project is primarily based on deferral to Andrew Snyder-Beattie and Ethan Alley, from whose post we got this idea.
If I were to make a decision now about whether Rethink Priorities should try to incubate a new project in this space, I would say that it should not . (Incubating a new project might involve things like scoping out a concrete project plan and conducting a founder search; more on how we think about project incubation in this post.)
The key reason is that there are a number of other actors already doing or planning projects in this space that are likely better suited to support this kind of work (primarily due to having more biosecurity expertise).
I think I’d be unlikely to change my mind about this bottom line with ~10 more hours of investigation, but could easily imagine myself changing my mind after something like ~40 hours of investigation.
More detailed summary:
There are two main types of PPE a project could focus on developing: Type I PPE, optimized for price and ease of use, and Type II PPE optimized for robust threat protection. I focus on type I PPE, mainly because it’s more commonly brought up in the x-risk community (but there are also some plausible object-level reasons to do so). (more)
I think the most important impact of type I PPE from a longtermist perspective is to reduce panic, unrest, and conflict in a highly deadly pandemic, thereby helping to avoid civilisational collapse. (more)
I estimate that the financial cost of a project aiming to develop a cheaper, easier-to-use positive pressure suit (a specific kind of type I PPE) would be $30 million, with a 70% confidence interval of $10-50 million. (more)
I estimate, primarily based on deferral to Andew Snyder-Beattie and Ethan Alley, that developing such a suit would have a cost-effectiveness equivalent to “buying” a basis point x-risk reduction (i.e., a 0.01 percentage point reduction) for 27 million, with a 70% confidence interval of $1.8 million to $260 million. However, I don’t place much weight on this model as I have significant uncertainty about both the inputs and the model itself. (more)
I think this project has other important upsides, including having low downside risk, being easily pilotable, and being a legible success for the EA community. (more)
I think there is already significant time and money being invested in this by both EA and non-EA actors who have a comparative advantage over RP in working on this project. (more)
My most significant uncertainty regarding the value of developing super PPE is to what extent there are significant bottlenecks to impact after development (e.g., in manufacturing, stockpiling, or securing commercial demand); it is plausible to me that working on those bottlenecks is more of a priority than working on PPE development. (more)
What is this project?
The project is to fund the development of better personal protective equipment (e.g., respirators, glasses, gloves, and full-body suits) for pandemics. The project could also involve funding stockpiling such equipment, or lobbying for the government to stockpile it, once it’s been developed.
There are at least two potentially high-impact kinds of PPE that the project could focus on developing, which I will arbitrarily call Type I and Type II PPE:
Type I: PPE optimized for being cheap, easy to use, and built from widely available materials so production could easily be scaled up, while still being highly protective.
There are various types of type I PPE one could try to develop – with various levels of protection.
Several people I talked to thought the highest priority type I PPE to develop was better and cheaper powered air-purifying respirators (PAPRs), which only protect against airborne pathogens.
Another option would be developing a positive pressure suit (PPPS) (which is among the most protective PPE currently available) that is easier to use, more comfortable, and less expensive than current models (e.g., BSL-4 suits, which require specialist training to use, get very warm and loud, and costs $2000 per suit).
Type II: PPE optimized for being as protective as possible while also being highly durable and not requiring electricity so they could be used in a wider range of GCBR scenarios (e.g., collapse scenarios). Price and ease of use are less important.
Some possible directions for this type of PPE could be: Making even better air filters, for example using electrostatic nanofiber; making existing PPE extremely reusable and durable; and combining state-of-the-art PPE for biological, chemical, and radiation threats.
(It’s also possible that one could develop PPE that has all of the above desirable features, i.e., being as protective as possible, cheap, easy to use, comfortable, durable, reusable, and electricity-free; but, at least in the short run, there will likely be trade-offs.)
The rest of this speedrun will focus on Type I PPE. There are three reasons for this:
Type I PPE has some significant-seeming benefits over Type II PPE, such as likely being more easily pilotable, more tractable, cheaper, and having more paths to impact.
(Perhaps for those reasons) My impression is that this is the type of PPE most frequently discussed in the biosecurity community.
I only realized that type II PPE might be worth developing late in the process of writing the speedrun, so I didn’t have as much time to investigate it.
Paths to impact
Note that in this section, I focus exclusively on how this project could help prevent existential risk. I don’t consider other types of impact, even important ones such as lives saved in the short term in a pandemic. This is because my team generally operates under a longtermist worldview, and under this worldview, effects on existential risk seem likely to be the most important effects in determining the expected impact of a project.
I tentatively think that the most important way in which type I PPE can help prevent x-risk is:
Help prevent civilizational collapse through (very roughly) the following path:
Investment leads to the development of type I PPE.
Governments stockpile large quantities (e.g., enough to cover ~10% of their population for 6 months), and/or markets are quickly able to ramp up commercial production in case of a pandemic.
In the event of a potentially catastrophic pandemic, all frontline medical personnel and essential workers that can’t work from home (e.g., essential production and delivery, electricity, relevant scientists) wear this PPE. The key effect of this is to prevent panic and unrest resulting from a lack of essential services. This prevents a situation where risk factors (e.g., pandemic + famine + conflict) compound in a way that results in collapse.
Other potential paths to x-risk reduction (very roughly sketched):
The more people wear high-quality PPE during a pandemic, the more people survive (both as a result of wearing the PPE and because of services provided by PPE-wearers), and the less likely the pandemic is to cause extinction.
In a collapse scenario, because people with essential jobs wore high-quality PPE during the pandemic, more people with essential skills for civilizational recovery (e.g., medical personnel, people working with producing food and other essential goods, scientists) have survived; this increases the chance of recovery.
Better PPE makes more medical personnel willing and able to do front-line work during a pandemic; this increases the chance that this personnel gathers useful information about the disease in question that can be used to develop a vaccine, treatment, or cure.
Members of the EA community gain experience, network and credibility, especially among policy makers and engineers, for developing a tangible and uncontroversially good product, which enables more effective and collaborative future work related to biosecurity.
Cost (~70% confidence interval at $10-50 million; median $30 million)
Note that I make a few simplifying assumptions in this and the following section:
Some alternative versions of this project are probably cheaper and less protective (e.g., developing a better powered air-purifying respirator) while others are probably more expensive and more protective (e.g., developing ten different products).
I assume that if this PPE was developed, it would “catch on”, in the sense that governments would stockpile sufficient quantities and/or commercial producers would be prepared to scale up production sufficiently quickly for this PPE to be effective in a pandemic.
So, my estimates ignore potentially major costs such as development costs, stockpiling costs, or costs of lobbying governments to stockpile.
Under these assumptions, I estimate a cost of $30 million, with a 70% confidence interval of $10-50 million.
Andy Graham and Tom Milton estimate that a final product could be reached in 2-5 years; because of the planning fallacy, I’ll up this to 3-10 years.
They don’t give details on how large a team would be needed. I’m going to assume an average team size of 10 senior researchers, and that the cost per researcher (including salary, benefits, office space, hiring costs, etc.) would be $150,000/year.
So personnel costs would be $4.5-15 million (3x10x$150,000 to 10x10x$150,000).
For equipment costs, I’m going to assume that the team would require materials equivalent to producing 100 prototypes, and that materials for one prototype would cost the equivalent of buying a BSL-4 suit, which is approximately $2000 (e.g., here). This would put equipment costs at $200,000. This seems way too low to me.
That would put the total cost at $4.7-15.2 million. This seems low to me.
It also seems low when comparing to analogous R&D projects:
DARPA contracted for $19.3 million to develop lightweight and adaptable military PPE in 2021. This seems relatively analogous in that the aim is primarily to adapt existing technology into a more user-friendly product.
(NASA has spent $420 million so far developing their newest space suits, and has contracted for a further ~$3.5 billion. But this doesn’t seem like a great reference class, since developing a space suit is probably more like developing type II PPE (involving more technological rather than design development), and maybe also expensive space travel.)
So I’m going to somewhat arbitrarily up the estimated costs to $10-50 million, and interpret this as a 70% confidence interval given that I have significant uncertainty about this estimate.
Cost-effectiveness Guesstimate model (70% confidence interval: $1.8 million to $260 million per basis point x-risk reduction; median 27 million)
Using the same simplifying assumptions as in the previous section, I made a first-pass, extremely rough guesstimate model of the cost-effectiveness of developing type I PPE.
If this median holds, this seems like very strong cost-effectiveness given our roughly estimated cost-effectiveness bar.
However, my estimate is extremely uncertain. In addition to the wide confidence interval, the output of the model varies significantly with each refresh (including, occasionally, negative numbers and numbers up to ~10x higher than the reported estimate). This is presumably because some of the inputs have such wide confidence intervals.
2 of 4 inputs in the model are based on deferral:
For “How much PPE would reduce existential biorisk in relative terms“:
Andrew Snyder-Beattie and Ethan Alley estimate that super PPE would reduce catastrophic biorisk (which I interpret as existential risks from pandemics) by >1% in relative terms. I don’t know if this estimate takes into account the probability of super PPE being manufactured and/or stockpiled at scale.
Based on this, I set a ~70% confidence interval of 0.5-5%.
For “Existential biorisk”:
On Michael Aird’s database, the recorded estimates of the existential risk from pandemics this century range from 0.0002% to 3%. I interpreted this as a 70% confidence interval, since it seems reasonable (though maybe a bit high) to think that there’s a 70% chance that current recorded estimates capture the true risk).
I think this model has pretty serious limitations and it plays only a small role in my views on whether or not RP should try to incubate projects developing super PPE. Some of these limitations are:
The input “How much PPE would reduce existential biorisk in relative terms“ is essentially a black box of deferral. This means that:
The model doesn’t do any work in unpacking how developing super PPE might reduce x-risk and what the key steps are.
The reasoning behind the point estimate is not transparent and so hard to evaluate.
The model should not be seen as much additional evidence on top of Andrew Snyder-Beattie and Ethan Alley’s original post suggesting this idea.
I think it’s likely that my interpretation of Andrew Snyder-Beattie and Ethan Alley’s post is off in some significant way, e.g.:
Maybe they use the term “catastrophic biorisk” to mean something less extreme than existential risk, in which case my estimate would be too optimistic.
Maybe their statement that most of the interventions in their original post “could reduce catastrophic biorisk by more than 1% or so on the current margin” was intended to mean that 1% is something like the upper bound, in which case my estimate would be too optimistic.
Maybe they factored in the probability of development being successful (in which case my estimate would be too pessimistic) or didn’t factor in the probability of adoption (in which case my estimate would be too optimistic).
My cost estimate could be significantly (order of magnitude) too low due to not including costs associated with adoption, such as manufacturing and stockpiling costs, as well as the opportunity cost of labor.
One person I talked to, Aman Patel of Technologies for Pandemic Defense, believes with ~80-90% confidence that the biggest barrier to impact for PPE is low demand for high-protection PPE such as type I PPE (but that such PPE could and would be developed by “standard” commercial actors if there was demand). If true, developing better PPE would not have much impact without significant further efforts, e..g, lobbying governments to stockpile PPE and integrate improved PPE into its preparedness plan.
Because of this, Aman believes with ~70% confidence (and it seems plausible to me) that actors in the EA space should not focus on technological advances, as he thinks this is likely not the comparative advantage of EA actors. Instead, he thinks EA actors should focus on securing demand, ensuring effective stockpiling, and evaluating how well PPE protects against GCBR-level pathogens.
At a very general level:
I’m reasonably but not super well-calibrated, and have no domain-specific evidence of how well-calibrated I am. So, on base rates, I think the model is likely overconfident.
I don’t have much practice with Guesstimate, so it’s possible that I’ve made technical or other basic errors.
Bottom line: This project seems to me to have few and relatively unserious (i.e., either unlikely or insignificant) downside risks. I also consider the willingness of top people working in biosecurity to talk about this project publicly as some evidence that the downside risks are likely relatively low, given the norms around infohazards in the biosecurity community.
Here are the downside risks I’ve thought of so far, in order of how important I think they are:
Super PPE could increase the likelihood of bioweapons attacks because the attacking side could protect themselves.
An especially bad variant would be if a malicious actor stole government stockpiles of super PPE, leaving governments defenseless. This could lead to a malicious actor gaining power and causing lock-in of bad values.
Even in the absence of super PPE, attackers could protect themselves via vaccinating their populations; but super PPE could be a cheaper and easier (but less secure) way to protect yourself.
But: Super PPE would also improve defense against bioweapons attacks; so the overall increase in the risks from bioweapons attacks seems small at best.
Especially Type II PPE could contribute to an arms race because it is perceived by an adversary as being developed for the above purpose (e.g., that it is being developed/stockpiled to protect the military in a planned bioweapons attack).
This risk seems especially pertinent if the government is involved in the development or stockpiling.
But: This risk seems relatively low; PPE seems pretty far down on the list of things that would contribute to an arms race dynamic. It also seems possible that PPE development would deter against bioweapons development.
Developing super PPE requires some technological development, which could be misused (e.g., better understanding of pathogen spread mechanisms could be used by malicious actors designing engineered pathogens).
But: The risk seems low – the main challenges seem to be design/engineering challenges with no obvious misuse potential.
The project would probably increase awareness about the inadequacies of present-day PPE, which could constitute an infohazard by motivating and spreading information about vulnerabilities to malicious actors designing engineered pathogens.
But: The risk seems very low – malicious actors will likely have thought about the state of existing PPE already, and the project doesn’t need to be very public.
Super PPE could give governments or labs a false sense of security regarding pandemics and make them complacent about additional prevention measures.
But: It seems about equally likely to me that the project would increase awareness about biorisk in government and therefore increase investment.
Pilotabilty and feedback loops
Seems like a project with unusually good feedback loops – it’s easy to see if the product is working as intended and if it’s easier to use than alternatives (you can just ask potential users, or see if e.g., governments and medical personnel adopt your product).
Seems relatively easy to pilot – a team could likely get significant information about the promisingness of the project in a short time (e.g., a year).
The kind of expertise required to make progress is well-known, and there are experts specifically in PPE development.
Material inputs are clear and, according to my estimates, not absurdly expensive.
One could put together a team with relevant expertise, acquire materials for a certain number of prototypes, and assign a short deadline to review progress.
Other actors in this space
Bottom line: There seems to already be:
Significant experience-weighted EA time invested in researching super PPE,
Significant government funding invested in developing super PPE, though with unclear (and I would guess medium-low) relevance for x-risk reduction,
Some experience-weighted EA time invested in developing super PPE.
Some experience-weighted EA time invested in securing demand for super PPE.
This makes me less excited about RP incubating additional projects in this space, as:
Low-hanging fruit are likely to be picked by other actors in this space,
We (Rethink Priorities’ GLT team) would likely need to do significant researcher up-skilling (or new hiring) before being able to significantly add value, which makes me think it’d be better for other actors in the space to take on this role.
However, I think there’d still be some benefits to incubating additional projects attempting to develop super PPE, including increased competition in the space, info value for other actors, and having more (semi-)independent chances of success at developing super PPE.
Finally, there being other actors in this space don’t really affect my view on whether RP should provide fiscal sponsorship to existing initiatives.
Below is a list of actors in this space that I’m aware of. I’m hoping this list might be helpful in (a) ascertaining the neglectedness of the area, and (b) providing pointers for people interested in working in this area. The actors on this list do not necessarily endorse or agree with the views I have expressed in this post.
Andy Graham and Tom Milton, two engineers, are running a feasibility study and, if the results look promising, planning to work on developing super PPE relevant to GCBRs. Their current plan is to focus on developing better positive pressure PAPRs initially, then potentially expand to develop a full body suit.
The Open Philanthropy Project is planning to do further investigation in this area.
Nadia Montazeri, a SERI research fellow, is writing an academic article on PPE for GCBRs (as far as I know the first article to name the distinction between type I and type II PPE).
Technologies for Pandemic Defense, led by Aman Patel, is working on creating an advance market commitment for PPE.
The Sculpting Evolution Group at MIT Media Labs is doing ongoing work related to PPE, including work on mapping essential workers to aid effective distribution in a GCBR event, advocacy to include more PPE in national stockpiles, and alternative sterilization methods for next generation PPE.
Charity Entrepreneurship has done a shallow investigation of super PPE, with the aim of identifying whether and how a charity could accelerate its development and use.
The Center for Health Security has been working on PPE advocacy for over 10 years, and is currently focusing on next-generation respirators.
The NextGenPPE group at Iowa State University is working on PPE development.
“Some early stage design/prototyping on a PAPR concept has been completed by Cass Springer”, according to this post by Andy Graham and Thomas Milton.
DARPA contracted for $19.3 million to develop lightweight and adaptable military PPE in 2021. (This might be of limited relevance to EA goals because the resulting PPE would likely be accessible only to the US government.)
The Biden administration has reserved $40 million for the development of pandemic countermeasures, including “next-generation PPE” (proposal here; approved on June 30 2022). I don’t know how much of the budget will be spent on PPE development. Naively, I would guess that the outputs will be only of limited relevance in GCBR scenarios, as I am guessing that GCBR-relevance is not considered a key priority of the. On the other hand, the US government had access to a report from the Bipartisan Commision on Biodefense prior to confirming this spending, which includes recommendations for “next-generation” PPE that sound relatively GCBR-relevant.
I heard about some additional promising early-stage projects that preferred not to be included in this list.
Once a relevant product has been developed, what are the key steps to ensuring it would be used in a pandemic? Are there key bottlenecks in manufacturing, stockpiling, or demand? Those bottlenecks could (a) potentially be more significant than the bottleneck of developing super PPE, and (b) imply that my cost-effectiveness estimate is too optimistic. (see the “Cost-effectiveness Guesstimate” section for more details on this uncertainty)
How effective should we expect super PPE to be against the worst engineered pathogens? How protective is current state-of-the-art PPE against the worst engineered pathogens?
What is the total existential risk stemming from pandemics this century? This is a key number in my guesstimate model and I feel like my estimate is an area where I could make quick improvements.
I had helpful conversations with Nadia Mantazeri both while and after writing this speedrun, and much of the framing and object-level information in this post comes from those conversations. I also got helpful input from Tom Milton, Aman Patel, Andrew Snyder-Beattie, and others, as well as my colleagues Renan Araujo, Michael Aird, and Linch Zhang (the latter of whom spotted a crucial error in my cost-effectiveness estimate). All remaining errors are my own.
This research is a project of Rethink Priorities. It was written by Marie Davidsen Buhl. If you like our work, please consider subscribing to our newsletter. You can explore our completed public work here.
Regardless of my bottom line, we would have conducted further investigation before deciding to try to incubate a new project in this space. My bottom line here is my guess about what my view would be after further investigation, rather than an assessment of whether we are ready to try to incubate a new project right now.
Credit to Nadia for coming up with this distinction, which she originally labelled as “vanilla” and “kinky” PPE, respectively.
Suggested to me by Nadia.
At the time of writing, Andy and Tom no longer believe that this is the highest priority type of PPE to develop – they have shifted their immediate focus to a positive pressure PAPR without a full body suit (though they note that a compatible body suit should be developed later).
Tom kindly shared with me a quick cost estimate of his own (after I made mine), which has a very similar range of $7.4-56.5 million, though the inputs are quite different (and probably more accurate). For developing a better PAPR, Tom estimated a 2-5 year timescale, a mean team size of 15, a mean cost per team member of $90000/year, equipment costs of $0.5-1.5 million, and other costs (e.g., trials and marketing) of $0.5-20 million. For developing a better PAPR and a compatible PPPS, Tom estimated that the costs would be twice as high, resulting in the estimate of $7.4-56.5 million.
Tom noted that some of these projects are likely much less efficient than a targeted project aiming for cost-effectiveness.
Since the output of the Guesstimate model varies each time you refresh the page (because of the inbuilt randomness), I refreshed the page 11 times and used the median estimate.
Or, more precisely, for a list of 6 projects, they say “We think most of them could reduce catastrophic biorisk by more than 1% or so on the current margin (in relative terms).” I’ve assumed that this estimate applies to super PPE.
Though Nadia notes that the content of government stockpiles is highly confidential.
Tom notes that this might not be entirely true as “testing of PPE is not particularly well-developed and the standards that exist are likely inadequate for GCBRs.”
For all not-currently-public information, I got permission from the project owners to include it in this list.