Epistemic status: Building a better gears-level understanding of why antivirals don’t work very well, explaining why portfolio construction for technology isn’t the same as investing in markets, then speculating on implications.
Note: Crossposted to Lesswrong

The public conversation around COVID-19 response, especially pre-vaccine, prominently featured the idea that there are treatments which we just need to find. The claim is that if we found good, broad-spectrum antivirals, we could treat COVID. 

But there is no guarantee that the thing we’re looking for exists. We might be searching up and down the street, under the lamps and elsewhere, for keys that are figments of our collective hopes and imaginations. There are words that describe things that do not exist. Like unicorns. Or antigravity. Fortunately, antivirals definitely exist. They just aren’t what I assumed when I was looking into the issue. And investing in them seems like a less promising avenue than I assumed. 

NOTE: I am not arguing against any investment in antivirals. I’m discussing the relative promise and synergies or anti-synergies of the approaches for fighting a pandemic.

Antibiotics versus Antivirals

Antibiotics, i.e. antibacterial drugs, are definitely a thing. Actually, around a dozen things. They prevent basic things that bacteria need to do, such as forming cell walls, using a specific protein synthesis pathway, or unwinding their DNA to replicate. Thankfully, some of the things bacteria need to do are unique to bacteria - their cell walls are different from animal cell walls, so interrupting formation of bacterial cell walls doesn’t kill human cells. Other things are the same. Protein synthesis and DNA unwinding are critical for human cells, but they happen inside of the cell, so we can use drugs that human cells keep out, but bacterial cells don’t. Those drugs are a bit more toxic, but if you need to kill off bacteria, sometimes it’s worth it.

Viruses are different. They use our cells to replicate, so they don’t do many things which human cells don’t. There just aren’t as many targets - and interfering with the ones that exist are more likely to hurt the human hosts. 

We want to find a useful antiviral, but we have good reasons to think that safe ones might not exist.

To be clear, we know of drugs that are effective at fighting viruses. Idoxuridine was the first antiviral, in the 1960s, and it is effective in fighting herpes. And by fighting, we mean slowing replication. It doesn’t actually eliminate herpes - nor do the other newer antivirals used for herpes and related viruses. Humanity had great success in finding cures for HIV. And by cures, we mean semi-toxic combinations of drugs that when taken indefinitely, slow viral replication enough that the hosts can live indefinitely and, due to very low viral load, not spread the virus. The drugs take months to work, but they are effective enough.

Other, newer antivirals fight things like influenza. Maybe. But not well. So where are we pinning our hopes, and why are we pursuing antivirals(1)?

Value of Information versus Portfolio Construction

I want to be incredibly clear; looking for antivirals is worth the money spent. 

We spend a few tens of billions of dollars per year looking for them, we learn more about viral biology and immunology, and we can treat HIV and herpes better. We might even find new treatments for other diseases. Value of Information here is really hard to compute, but it seems pretty high. At the very least, we have no fundamental reason to think we won’t find something that works.

But in constructing portfolios for investment, we aren’t just looking for positive returns, we are looking for a coherent plan, hopefully with synergies and risk mitigation. Unlike financial investments in the market, there are places where investing in one technology accelerates our returns in other places, or unnecessarily duplicates effort and wastes money, or actually makes success impossible. 

If we’re in the stock market and banking stocks are highly correlated, splitting our money among them is typically a bit better than investing all of it in any one, because we’re diversifying, with little or no cost in terms of returns. If we want to eliminate malaria and spend half our money on bed-nets and half on gene-drive mosquitoes, we mitigate risks of either approach, but they aren’t complementary or even parallel. Instead, there is likely to be wasted effort. If we’re SpaceX and invest in reusable spacecraft and also batteries for ion drives, we’re probably wasting the money on batteries. They aren’t compatible with the approach we’ve picked. And if we’re building a PC and invest half our money on an awesome graphics card, and the other half on a huge SSD, we end up with no CPU, and we’ve wasted all of our money by failing to get everything we need.

The above examples are talking about very different strategies, in different domains, with different failure modes. Which one seems to describe investing in antivirals alongside other parts of pandemic response?

Applying Portfolio Theory to Antivirals

I’m not sure exactly how this applies, but the new 100-day plans for response seems to be either split-the-money, and hope one approach works, or pick-incompatible-approaches, waste lots of money. Why?

If effective vaccines are available in 100 days, and we can scale up manufacturing, the game is over, we win. Treatment of the cases that happen later is either useful as a mitigation measure to slightly reduce impact, or a backup plan in case we don’t manage to make vaccines.

Perhaps these are independent resources, and we can spend money and research effort on antivirals without reducing the investments in vaccines? That seems implausible. Budgets are limited, and vaccine manufacturing is expensive. An extra couple million dollars might only expand production of vaccines by 5%, but if antivirals and vaccines show up at the same time, per the 100 day goal, that’s probably a better investment than antivirals.

Conclusion

Please correct me if I’m wrong on any of this. Otherwise, I’m interested in figuring out what we should do differently in the future for pandemic preparedness on the basis of this partial/tentative analysis.

 

  1. An aside: The investment in antivirals isn’t confusing as an outcome. There are reasons that vested interests push for the approaches they can make money with, and reasons for both clinicians and regulators to push for better treatments, even if they are only marginal improvements or are unlikely to succeed. There is no guarantee that markets pursue socially optimal policies - quite the opposite. So this is an expected failure mode.

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13 comments, sorted by Highlighting new comments since Today at 3:57 PM
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Hey David, thanks for the post, always healthy to hear ideas about what not to do. I have a much more positive view of the promise and importance of antivirals for future pandemics, broadly for the following reasons.

Biological diversity & over-updating from one disease

COVID-19 vaccines have been exceptionally successful, in fact surprisingly effective to the expert community. It appears that COVID-19 is a disease that is (1) sufficiently immunogenic to elicit strong and lasting immunity, (2) was readily adaptable to the new vaccine platforms, thanks to prior research with SARS-1, and (3) shows sufficiently low antigenic variation that vaccines remained effective so far (thanks to its for respiratory RNA viruses unusually low mutation rate).

These properties do not hold for all viruses. For example, for the HIV pandemic vaccine development has been very unsuccessful, and antiviral development highly successful.

One under-appreciated theme in biology is that living systems can show unexpected behavior, and observations from one example often do not generalise. The success of COVID vaccines implies that vaccines (if we can speed up clinical testing and manufacturing) can be a powerful pandemic defense. It does not, in my view, imply that they will be a sufficient defense against most or all possible threats.

Future promise of antivirals vs current performance

The absence of success stories to date is not evidence that a promising technology under development will not be successful - this is the nature of tech development. (E.g. mRNA vaccines didn't have such a success story until COVID, and we shouldn't have stopped developing mRNA vaccines in, say, 2015 because of the absence of successes.)

From a 'first-principles' look at the challenges of antivirals (as a biologist but without drug dev expertise), I am pretty excited about foundational research to accelerate their development.

a) Scale: the 'big win' would be sets of antibiotic-like therapeutics that wipe out a majority of viral pandemic risk; a close second 'platform therapeutics' to be made in response to new pathogens that can be deployed like vaccines

b) Tractability: several promising approaches are discussed in the literature - in brief (i) host-directed drugs that target human cell pathways that viruses need to replicate, (ii) virus-specific drugs (e.g. polymerases that are distinct from human polymerases, see HIV drugs) and (iii) drugs that tune the immune system in response to an infection (e.g. dexamethasone). No doubt it's much harder than antibiotics, but we have made much progress in bio and drug dev since the first antibiotic has been discovered in the 1920s too.

c) Neglectedness: infectious disease is - with the notable exception of HIV - not a problem in western countries. For this reason, antiviral research (like antibiotic research) has received much less attention and funding than other diseases (cancer, gene therapy, neurodegenerative diseases, ...). mRNA vaccines had the advantage that mRNA technology may also be used for cancer and other diseases, so I find it likely that antivirals are especially under-invested in the portfolio of medical countermeasures.

Portfolio theory and scientific innovation

In foundational (bio)tech development, I am pessimistic about our ability to 'pick the winners' at a high level. The history of biomedical research is full of examples of promising technologies that never succeeded, and others that were unexpectedly successful. A 'split-the-money' approach of diversification, in principle, will always be required at such success rate, though I grant that working out the relative % of investments is very hard.

Thanks so much for the excellent feedback. I've updated a bit, but I don't think we disagree as much as it seems at first glance, or I'm not understanding your position. In general, I think you're responding about antivirals in general, and I was talking about antivirals specifically as a response option for during a nascent pandemic. But I do see a few points of clear disagreement.

1) Biological diversity & over-updating from one disease

Antivirals work poorly everywhere. The "best" antivirals we have for flu, like tamiflu, don't have any significant clinical impact, according to all of the studies not run by the company making it.  And yes, antivirals are relatively more important for diseases that don't have vaccines, but as I noted, HIV antiretrovirals are weak and only work slowly and in combinations, and "highly successful" seems like a weird claim given how long it took and how complex it is.

And I agree that vaccines aren't always practical for all diseases, at least yet. But that doesn't lead me to think that we might be successful with antivirals.

[Edit to add: "The success of COVID vaccines... does not, in my view, imply that they will be a sufficient defense against most or all possible threats."

No, but finding vaccines not working says nothing about the success of other approaches - nothing guarantees that anything works, so pessimism on one front doesn't justify optimism on another, even if it causes us to invest differently.]

2) Future promise of antivirals vs current performance

I think I agree with all of this, which is why I think antiviral work should continue to be funded. But none of this makes me think it's a valuable target for emergency response.
  
3) Portfolio theory and scientific innovation

Agreed on our inability to pick winners, and the difficulty of exactly choosing relative investment amounts - but again, I'm not talking about foundational research, where a diversity of approaches are really important, I'm talking about last-ditch emergency response. We need more and faster COMPARE-like trials for extant treatments, but new drugs seem like a dumb place to put money if we need results this year.

What about the use of antivirals to prevent infection, in the form of pre-exposure or post-exposure prophylaxis?

The reverse transcriptase inhibitors (e.g. Truvada) used for HIV PrEP (Pre-Exposure Prophlaxis) seem to also work for (treatment of) Hepatitis B. If we had platform pre-exposure prophylactics, wouldn't that complement vaccines, or perhaps be useful for stopping outbreaks of diseases that are harder to develop vaccines against?

These pills have enough side effects that we're not going to ask large groups of people to take them on a regular basis unless they're genuinely at risk of exposure, but that would be true in a pandemic. At least with HIV, it also seems like taking antivirals in the 72 hours after infection[1] is pretty good at preventing infection. That seems like the sort of thing that could bring R_0 down?


  1. I think this also means that your note that "the drugs take months to work" is not quite accurate, at least for this use case ↩︎

That's a good point. I seem to recall that the efficacy of (most) antivirals as prophylaxis against most diseases is approximately nil, and we can't easily do COMPARE-style studies for prophylaxis, so I'm unsure if, in general, this is a good strategy. (And I don't think HCTs for trying this out early on using a battery of drugs would be ethical, even ignoring sample size requirements, though perhaps animal studies could be done quickly.)

But I definitely think post-exposure prophylaxis is potentially promising, if it's likely to work. The two challenges are that 1) it requires contact tracing far better than what we saw during COVID - though we often manage such contact tracing for HIV, so it's not at all impossible, and 2) in most countries, I can't imagine that the prescription / medical system would adapt fast enough to allow such prescriptions, short of them actually becoming super-competent at response. So if this is a good idea, we need lots of preparation to actually make sure it can be used. 

Alternatively, I guess it could be used very early on to slow / stop initial spread, but for the cases I'm most concerned about, I don't know how we'd know enough to try the strategy then.

One empirical subquestion I'm interested in (in case anybody reading this is very knowledgeable about human immunology, which seems plausible) is whether we have strong in-principle reasons to believe that our immune systems, with sufficient coaxing, is capable of producing antibodies for arbitrary diseases. 

This seems like a necessary but not sufficient condition for developing vaccines that work against arbitrary novel diseases, and may become increasingly relevant if we're more worried about manmade than natural pandemics. 

This is an interesting question which I have thought about a little before, but stopped given infohazards risks from thinking too hard about ways in which this might be possible outweighed the actionability of such insights. For a variety of reasons, which includes this reason, I am a fan of pushing fast response passive immunoprophylaxis platforms and other countermeasure approaches such as the receptor-competition based ones, it seems that whatever we are worried about, such approaches would be robustly good.  

Short answer (mostly based on undergrad immunology and vaccinology): yes there could be things.

 There are different potential reasons for why active immunisation might not work for a given pathogen, the most obvious one being that we cannot induce antibodies that manage to bind to (neutralising) areas on pathogens. This may be because of us only having a limited set of B/T cell receptor genes (and even less flexible MHC receptor (present pathogen peptides to immune cells) genes which might be relevant for inducing immune responses) which might mean that induction is difficult - but these genes vary across the population potentially exactly for the reason that the population is protected from getting wiped out by one specific pathogen. This is somewhat seen in HIV where some individuals are able to develop neutralising antibodies and most others don't - question is whether sequential immunisation with more and more complex antigens (to achieve antibody evolution to penetrate HIV glycan shields) can get us to neutralising antibodies for everyone or not. 

Another mechanism (discussed by Tessa)  might be that antibody-dependent disease enhancement. If any neutralising antibody induction by active vaccination is accompanied by non-neutralising antibodies which may cause ADE for a given pathogen this might be bad. I think this is somewhat a technical challenge, but there might be pathogens which feature unique mechanisms that make overcoming this very difficult. 

Not an expert, but Antibody-Dependent Enhancement (ADE) shows that we are not guaranteed to produce useful antibodies for arbitrary diseases. In fact, we can produce antibodies that make a disease worse!

This happens in dengue, where there are different serotypes of the disease and antibodies for one serotype can be non-neutralizing for others, but "original antigenic sin" (I find this term quite funny) means that we don't generate new ones and the infection is enhanced because the non-neutralizing antibodies recruit macrophages, which dengue likes to replicate in.

Here's a Derek Lowe post from December 2020 on ADE, which also notes examples in HIV, Ebola, and coxsackievirus. I was in fact a bit worried about ADE with SARS-CoV-2 early in the pandemic, since spike protein immunization against feline coronaviruses has sometimes led to ADE.

Definitely not expert enough to confidently answer this, but I thought the answer was obviously yes - I don't think there are any diseases where it doesn't happen as a natural part of response. (Even HIV is mostly fought off quickly, but in cases where it spreads, it infects enough immune cells that it persists and eventually destroys the immune system.)

So for example rabies has a ~100% fatality rate without vaccination, but immune systems are expressive enough to produce antibodies with vaccination.

I'm not personally convinced by directly empirical evidence that it hasn't happened so far -> this isn't possible, since the space of pathogens that's evolutionarily plausible is presumably a lot narrower than the space of possible pathogens, including engineered ones.

Great post, thank you. I hadn't considered the anti-synergy of treatment and vaccination explicitly before.

How much weight to put on the vaccine risks you mention in the following sentence seems very important to whether to fund anti-virals or not: "Treatment of the cases that happen later is either useful as a mitigation measure to slightly reduce impact, or a backup plan in case we don’t manage to make vaccines.".

At the start of this pandemic, most people thought vaccines might be very far off or impossible. I'm not sure how much to update based on exceeding expectations and ongoing with to shorten timelines. However, we seem to be quite good at testing therepeautics which seem to need less customising (hence easier production), especially when the side effects profile is well understood (eg the RECOVERY trial). While not an anti-viral, dexamethasone has probably saved a lot of lives. I don't know enough biology/medicine to be able to distribution how much we need to separate different classes of drugs.

Yes, treatments definitely ameliorate risks from not finding vaccines - but it seems that effective new treatments were far harder to find than vaccines.

And yes, clearly symptomatic treatment with extant drugs is important - dexamethasone, but also prone positioning, and basic parts of treatment like pulse oximetry and ensuring sufficient fluids. But these don't need 100-day crash research programs for new treatments, which is what was proposed, they need RECOVERY-like trials (perhaps more expansive, covering more parts of clinical care,) to start on day 1, instead of waiting months to start.

Could much of the problem be due to the difficulty of starting treatment soon enough after infection?

Given the failure of antivirals to work even prophylactically, and the fundamental issues I mentioned, I don't think that is the key issue.