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IDO Appears to Have Wiped Out

We have the answer to a question posed here earlier this month. That was after the Merck/Incyte failure of a combination of Keytruda and Incyte’s IDO (indole 2,3-dioxygenase) inhibitor. That mechanism was supposed to increase T-cell activity, but the trial showed it to have no effect on Keytruda’s efficacy at all. Earlier IDO trials had not gone well for other companies, but there had been hopes for this one.

Just as there were hopes for another inhibitor that Bristol-Myers Squibb had bought from Flexus (which is quite a tangled tale in itself). I wondered at the end of that last post if the Merck/Incyte failure meant that the BMS/Flexus effort was doomed as well – everyone who follows this area was wondering the same thing – but as some readers pointed out, the Flexus inhibitor did have a somewhat different mechanism of action, so there was at least a chance.

Scratch that. Yesterday, Andy Biotech noticed (and posted on Twitter) that the two Phase III trials had quietly been scrapped on So I think we can say that (at least as currently configured) the excursion into IDO inhibitors has been a costly mistake. And remember, as is almost always the case in these things, that it didn’t look like it was going to be any such thing. IDO inhibition made sense in terms of what we knew about its biochemical pathway and the workings of T-cells, which is why you saw several companies taking a whack at it (Pfizer was in the area as well, and there are others whose preclinical programs you never even heard about). All in vain.

There’s a great big central problem of drug discovery for you: how do we go into the clinic (but avoid spending Phase III levels of money) to find these things out? Better yet, how do we avoid developing such things in the first place, if they’re going to do this to us? Billions of dollars, literal billions, are stacked up waiting for anyone who can start to begin to do such things. Just to pick on a recent hyped-up press release, could BenevolentAI’s “machine brain” have warned people off? Would anyone have believed them if they had? (I doubt that very much, for both questions).

No, the problem is that we’re doing things that no one has tried to do before, and we’re doing them on what is clearly incomplete information. And the only way to make it more complete is to. . .go ahead and do those things,apparently, and at great cost. Could you have warned everyone, in convincing fashion, not to chase IDO inhibitors? CB1 antagonists for obesity? Cathepsin K inhibitors? Anti-amyloid antibodies? Mixed PPAR ligands? CETP inhibitors? Substance P inhibitors? Gamma-secretase inhibitors? And I’m just picking ones off the top of my head that had multiple large research organizations working on them – there are plenty more where that came from, especially if you just bring in the targets that were disastrous for just one or two companies.

All of these looked like worthwhile ideas at one point, and uncounted sums of money were spent on them (money from sales of other drugs to other customers and directly from investors). All of it could have been put to better use, but could you have done better? Sent people into areas that were less likely to fail, or found out that these mechanisms had something wrong with them without all the time, effort, and money? Come on down and try it.

46 comments on “IDO Appears to Have Wiped Out”

  1. Anon says:

    When you give up hope (on science) faith carries you further, and then miracle happens. Fair to say that was the guiding principle herein.

    1. anon3 says:

      Sirtirs was a platform, and never even had a molecule in phase 1 (I think). Not really the same thing.

    2. Philip Ahern says:

      I wasn’t aware that targeting RORgt had gotten that far. There are some good reasons to think of it as an ideal target, but enough things to make you worry too. One of the phenotypes of RORgt knockouts is massive reductions in Th17 cells (not just IL-17, but everything else), but they also develop “spontaneous” lymphoma too.

  2. anon3 says:

    Remember that pipeline blog about a review article that said that chemical synthesis and med chem are the rate limiting steps in drug discovery…

    1. tlp says:

      One of the authors is VP Drug Discovery for BenevolentAI menthioned just another day

  3. JB says:

    checkout galectin inhibitors in combo w/ immuno

    1. I’m assuming you’re referring to Galectin 3 inhibition?

      Early days, but I seem to recall the interim Phase I combo data offering a hint of promise. There’s also interest in Galectin 9 which plays a role in TIM-3 (a negative immune checkpoint) mediated immunosuppression.

  4. Magrinhopalido says:

    I agree 95+% with the central thesis of the post. But it should be noted that Tamas Horvath (Yale) said very early in the game that the CB-1 receptor was a bad target for obesity due to its influence on dopamine signaling/anhedonia. And he was right. Anhedonia was dose-limiting for taranabant – a very strong effort from MRK.

    There are probably other similar cases.

    If you play the percentages, you are always going to come out ahead by saying “This target is crap!”. But there are also some instances where in vitro or animal data suggested that the target was indeed crap but drugs made it to market and helped people.

    1. Derek Lowe says:

      That’s quite true. And there are surely others where the early data were discouraging, the project was dropped, but something good would have come out of it had it been pursued. But we’ll never know!

      The challenge is to not just sit there and say “That’s not going to work”, even though you’re right the great majority of the time. . .

      1. Anonw says:

        The most useless scientists r the ones who just say “that won’t work” to everything. We play long odds in research… most experiments fail (so to speak)

        1. DrOcto says:

          It’s the step after a failure that I find interesting.

          You did something in the lab because you thought it might work. When it fails, the question ‘why didn’t it work?’ is the most important one you can ask. I frequently come up with 2-5 explanations for a given adverse result (e.g. poor reaction yield/purity). Then it’s just a case of designing the experiments that can corroborate/disprove each theory.

      2. Michael T says:

        highly active treatment. Improvement on that is difficult. While Phase II results were promising, oncologist’s use and understanding of PD1 inhibition has progressed over the last 3 Not so sure that IDO inhibition is useless for the following reasons.
        1. Keytruda is a years, making the difficulty of add on therapy even more difficult.
        2. There was significant risk of using an IDO inhibitor as an add on therapy without knowing if the tumor was over-expressing IDO, since pre-screaning was not part of the inclusion criteria. Likely, it was posited that non IDO over-expressing tumors might develop this as as escape from PD1 inhibition. This appears unlikely at this point.
        3. While not ideal from both a commercial and clinical treatment view, a companion diagnostic to identify IDO over-expressing tumors would be helpful to identify patients who would most likely benefit from IDO inhibition therapy.

        While not quite dead yet, the road to success is neither straight-forward or short.

    2. anon says:

      I think one of the main issues related to the CB1 antagonist trainwreck, is that the drug developers asked the question “how do we make obese people eat less”, instead of asking “why do obese people eat too much for their own good, and why do they eat unhealthy food, even though they know it will end up killing them”.

      I think they asked the wrong question because it was easier to answer. The latter question is disturbingly similar to questions about addictions in general (alcohol, benzos, opioids, tobacco, etc.), and it seems reasonable to assume, that like many cases of addictions, serious obesity is often preceded and promoted by psychological issues. And we all know how hard it is to cure those with drugs.

  5. Exploitation of the IDO/TDO pathway might still turn out to be worth the effort (at least clinically, you can see the steam arising from evaporating commercial interest), but in the context of combination with conventional chemotherapy and/or radiotherapy, rather than being hamstrung through combination with first wave immune checkpoint inhibitors with inherently low response rate.

    Will be interesting to see if the earlier stage dominoes held by NewLink, Lilly and Kyowa Kirin will also join the tumble.

    1. Jim Hartley says:

      “You can see the steam rising from evaporating commercial interest.” Really excellent!

      1. I thank you. A collective $1 billion in upfront payments alone makes for a fair volume of vapour.

  6. anon says:

    “how do we go into the clinic (but avoid spending Phase III levels of money) to find these things out? Better yet, how do we avoid developing such things in the first place, if they’re going to do this to us?”

    At the risk of stating the obvious, maybe it would be a good idea to try and find out (even) more about the relevant biology, before sending the stuff to the clinic? Doing more target discovery, fish out more enzymes/proteins from the cellular soup, try to find out what they are, what is their function, how is their synthesis/modification/breakdown is regulated, discover more biochemical feedback loops, etc. Basic research into cellular biology.

  7. Magic 8-ball says:

    Could BenevolentAI have saved the day for IDO? No – it would have tracked with current working knowledge and hypotheses of biological pathways and cellular function(s), which is clearly incomplete. A magic 8-ball would have done better in this case. “AI” can only work if you can cleanly codify the system and if there’s plenty of good, robust data – i.e. not biology, as the field currently stands. Unfortunately, the destiny of many first-in-class, novel MOA therapeutics remains a crap shoot.

    Perhaps a better question to ask of BenevolentAI et al., is why IDO didn’t work, 20-20 hindsight of course. However, the AI answer or hypothesis would likely be unclear and would not be validated, but maybe interesting nonetheless.

    In the case of IDO, were there any tangible clues from preclinical, Phase 1, or Phase 2, that there was an iceberg waiting at the end of the line?

  8. Incyte pulls its collaborative pivotal combination studies:

  9. Chrispy says:

    It should not be possible for clinical trials to be “quietly scrapped.” If you get the go-ahead to put your drug into people, part of your obligation should be to publish those results no matter what the outcome. I can remember years of matrix metallo-proteinase research that repeatedly failed in the clinic due to musculo-skeletal rigidity — in the early days it was just whispers at conferences. Then, when I was at a big pharma, the FDA actually suggested that this might be something to explore as we brought our own MMP inhibitor forward — it had been observed in other trials that were not published but the FDA had seen. How many times have you speculated about why a trial was ended — liver tox? Was it on-target tox? Did they get coverage of the target? Nav1.7, too, had everything going for it as a target for pain, and yet it took years longer than it should have to realize that it was a bust. It should be part of the Grand Bargain made when entering clinical trials that the results, for better or worse, must be published in their entirety.

  10. BiotechFanatic says:

    The problem elegantly laid out by Derek is exacerbated by duplication of efforts as competitive pressures motivate pharma players to independently pursue identical targets – likely there is an element of fear-of-missing-out mixed in there and hence the total spend and effort expended on what ultimately turn out to be wasted efforts is duly amplified.
    Alas “duplication” can be justifiable to the extent that an individual pharma may not have the right molecule, at the right dose, in the right indication, with the right clinical drug design etc.
    Between these two factors, I find it hard to see a way out of the problem and predict continued duplication of efforts on MoAs that turn out not to work!

    1. MrRogers says:

      The larger shame is that those same resources could have been put into another target that might have worked. It’s like Exxon and BP drilling into the same reservoir. I sometimes wonder whether we wouldn’t be better off if the FDA were to auction off “leases” on specific target-indication combinations (probably at the phase I stage). Just like the mining and petroleum industry, the license could be traded. It could also be revoked for lack of progress (as in a mineral claim). If two leases were available on the same target, then companies could still compete with each other, but additional entrants would be prevented from coming in. You’d probably wind up with more careful target validation, you’d definitely save on patient adverse effects, and you might get real targets identified faster.

      1. BiotechFanatic says:

        Interesting idea. Perhaps the PD1/PDL1 space could have done with that a year or so back. Do we have any good examples of targets which multiple different parties tried to exploit, but only one or a handful managed to do so successfully? If so this would suggest there is some benefit to allowing many/or effectively unlimited access to such “leases”. If not, or if this is rare, the argument becomes much stronger.

    2. Nick K says:

      I’ve often wondered if companies could collaborate AFTER the collapse of a therapeutic hypothesis like this one in order to discover exactly what went wrong. Some good would at least emerge from the wreckage.

  11. Dave says:

    And it appears that the answer to the question: “Who pays for the failure?” is the American public in outrageous prices for those drugs that did not fail – given that other countries somehow manage not to pay those prices.

    1. Derek Lowe says:

      They are able to pay those prices because we pay the price we pay.

      1. milkshake says:

        the corollary of that is: why are the clinical trials so outrageously expensive? Those “non-profit” research hospitals sure charge outrageous fees. Phase one short study of a chemotherapy agent costs about 100k USD per enrolled patient. So 50 patients is about 5 mills. And they take the drug for only few weeks. Even just re-processing already acquired old clinical data into a format more agreeable to FDA cost my previous employer something like 30k per patient… Why nobody tries to make the cost of clinical trials cheaper, it disqualifies smaller companies starved of investment, they cannot get investors until they present clinical data, etc.

  12. Paramus says:

    Derek, I enjoy your blog and it has great information but I would love to see a post that explains your 3.18pm statement. Having lived in both the UK and US (12 years). High drug prices in the US are simply another symptom of a broken health care system where everybody gets rich at the expense of the patient. I doubt prices would come down if you stopped ‘subsidizing’ the rest of the world!

  13. MrRogers says:

    I’m not Derek, but I’ll give my perspective. Drug discovery is an expensive, risky business with long time horizons. To induce capital markets to invest in that business, a commensurate return must be available. Because of the way that European countries currently (don’t) pay for drugs, only a small fraction of the return necessary for the current level of drug discovery is available there. Instead, the lions share comes from the US. If the return available in the US were to decrease, discovery would decline and there would be fewer new drugs to buy. (And in that case there would be more pain, suffering, and premature death in the world.). Quite literally, Europeans can pay what they do because of what Americans pay.

    1. 2G says:

      Why is it so expensive in the US (compared to EU)? In the US you get sued whenever somthing works not well and pharma (deepest pocket) has to pay ridiculous compensations (to the lawyers)…

    2. Tlp says:

      I think it was discussed here quite many times that r&d expenditure is not the main factor for drug prices. C’mon, look at tecfidera. It’s all about alternatives costs. Each mega-expensive drug ‘saves’ money, just not patients’ money.

    3. Biotechie says:

      MrRogers is spot on. If drugmakers got the low returns that national health systems in Europe (or anywhere else in the world) are willing to pay for, then drug discovery and development would look very different. Innovative drugs just wouldn’t happen (at least the via the mechanism and via the entities that do it at the moment). The dirty little secret is that US taxpayers essentially subsidize drugs for the rest of the world. The US market is about the only market where manufacturers make the sizeable returns they need to encourage further investment (given the long timelines to market). Manufacturers look at the rest of the world as a write off. Places like India they hardly bother at all.

      The second dirty secret is that it yes manufacturers are trying to get the charge the highest amount the market will bear, but it is all the middlemen (e.g., pharmacy benefit managers and wholesalers and insurers) in the healthcare system that really account for the price inflation.

      The last dirty little secret is that drug prices (though unreasonably high in the US) are not the biggest factor in rising healthcare costs. It is hospitals, not drugs.

  14. Paramus says:

    The Americans save the world yet again, really!

  15. Kelvin says:

    “No, the problem is that we’re doing things that no one has tried to do before”.

    It seems the main problem is that we’re doing things that lots of people *have* tried to do before, and failed, but we’re not listening and think we know better. Hubris.

    What was that definition of insanity again?

  16. Robert says:

    I’m looking forward to seeing more data from IDO inhibitors – a company like INCY is seeing their IDO drug valued by the market at tens of billions of dollars.

    1. drsnowboard says:

      Not any more…

  17. Dominic Ryan says:

    There are exceptions to all categories below, but I think the main view is correct.
    What is pharma good at?
    -finding a molecule (large or small) that modulates a target
    -figuring out how to make it according to rules
    -testing it
    -getting it to patients

    What is pharma less good at?
    -peeling back basic biology
    -connecting that biology to human pathologies

    What does the success of what we are good at depend on?
    -The second group

    Where does the second group come from?
    -Largely academic research

    What is a pharma to do?
    -Lock up as much of the second group as possible, before your competitor does!
    -Sometimes at the expense of truly understanding it.

    Why do academics do that?
    -Bayh-Dole didn’t get it right. Universities have a vested interest in pushing early discoveries into IP as fast as possible. Companies have a vested interest in locking it up as fast as possible. All that happens despite not really knowing the whole story. Remember, you can file IP on junk. You can apparently get a patent issued that is later killed, likely because the bar was too low and USPTO over worked. The point is that IP is not a measure of scientific depth or even truth.

    What’s to be done?
    -Public research funding needs to do more to shore up translation, perhaps around fewer areas if dollars are spread too thin, but at the moment pharma is bleeding cash on long odd bets.
    -The public is already paying for that in higher prices for health care, not just drugs. Industry needs to do more to explain that at all levels but perhaps especially the non-expert and non-government officials: the soccer dads and coal miner moms.
    -Bayh-Dole needs to be amended to move the bar out on what constitutes progressable ‘discoveries’. I suspect even universities would agree. I think the number of tech transfer offices that make money is a small minority.

    1. Nick K says:

      All true, but don”t forget the poor quality and reproducibility of so much biomedical research.

  18. KS says:

    Apparently no one on this blog has brought up the central question to IDO1 inhibition: Was there a robust clinical PK/PD relationship in drug exposure and inhibition of kynurenine production in tumors? I wonder if Incyte has this information on epacadostat and BMS as well, but they just haven’t shared.

  19. exGlaxoid says:

    Clinical trials are expensive because companies have no alternative (other than selling the drug as a nutritional supplement) and the FDA and politics have lead them to demand large and long drug trials, which have quickly diminishing return after a few dozen people. If we allowed faster trials with fewer people to start, we could lower the costs, as was common in the 1970’s when many drug trials took months to start and a year to complete. And lawyers have sued every drug company for everything that they can get away with.

    The combination of politicians, lawyers, and bureaucrats have made it so difficult and costly to get a new drug approved that many companies have abandoned compounds that might have been better than what exists, but they don’t want to to take the risk of losing money, which is likely for any drug that is not a block buster. I took part in a tiny drug trial years ago for a new formulation of an existing, well known drug for a new use, and the FDA made every step a nightmare for both the patients and the small company. What should have taken a year was spread out for 10 years and the company eventually went broke, as the FDA dragged its feet.

    I understand the need for safe and effective, but they often go far past that mark. Just like Avandia was dragged through the streets for being unsafe, when the final data on that is far from conclusive, but yet many people are still dying of diabetes daily, which is the risk of NOT having new drugs. I see more people die of not having any drug available for their issue than I do from having a drug that does not work well. Of course, generics are still widely used, as harder to sue them, and I would guess that 90% of all drug issues from them, but lawyers stay away as not as lucrative a lawsuit to sue a generic company.

  20. steve says:

    With regard to IDO inhibitors, the issue is assuming that a single intervention will overcome tumor suppression. I think we were lucky with PD1 inhibitors. Tumors have a plethora of redundant defenses. Knocking out IDO and expecting cures is a bit like thinking you can grab the football just because you got past the first defensive linesman. Or maybe better, that you can grab the football when you’re sitting in the top tier of the stadium and was able to move to the next row down.

  21. anon says:

    The IDO story is more than 20 years old. The in vitro study initially published by Munn was very solid. I am sure most of IDO inhibitors are potent in short term in vitro and in vivo mouse testing. However, the challenge for industry is how to translate these results into real benefits in a chronic treatment. Unlike small molecules that can induce acute responses, modifying an elastic immune system in a chronic way alway confront risks of desensitization.

  22. Anne M Mills says:

    One of the huge problems with all the existing IDO trials, in my opinion, is that they have failed to incorporate biomarker expression as a criterion for study inclusion. Having now studied this marker in a variety of cancers, I can tell you that most tumors are entirely negative or only focally positive. BUT, is a subset (roughly a third of triple-negative breast cancers, for instance, as well as plenty of MMR-deficient endometrial cancers and some NSCLC), which are beautifully positive. Often this positivty runs with PD-L1, making it a plausible mechanism for anti-PD-1/PD-L1 resistance in these patients. It’s a shame that these patients might never have the opportunity to benefit from these drugs because the trials were designed without consideration of tumor pathology. As we gain the ability to administer increasingly complex drug combinations, rational patient selection is going to be the name of the game for immunotherapy, not a blanket approach which is sure to result in lackluster results, wasted resources, unnecessary side-effects… and lost opportunity among the potential responders. Here are a couple of our recent studies on this topic:

  23. colin j macdonald says:

    Incyte/IMV phase 1/2 Ovarian The early results show best in world results ( 70% disease control ) How interesting might that be?

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