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Rules for Modern Drug Development

Here’s Robert Plenge at Merck, writing in Science Translational Medicine on what currently looks like the best way we have to do drug discovery. I’ll freely admit that I didn’t expect this article to be as good as it is (a lot of things with titles like this are crap). But he’s done a good job of laying out what you need to have the highest chances for success, and it’s good to have all of this summarized. He outlines four key features:

1. You need evidence from human biology before you even start. For infectious diseases, that’s pretty obvious, but for a lot of other targets, not so much. Careful study of human genetics and rare mutations can tell you a lot – if you have an idea for some protein as a disease target, it’s time to see if anyone has ever had the misfortune to be born with loss-of-function.Do not, Plenge warns, use animal models to pick or validate targets up front in the absence of evidence from humans beings or (at the very least) human tissues or cells. This requirement makes it very hard going in some disease areas, but that’s one of the points: those disease areas are going to be very hard to make progress in.

2. Your proposed target is going to have to be amenable to being modulated, and a lot of them aren’t. Gain-of-function on an enzyme, for example, is quite rare, unless you’ve got a bounce-shot inhibit-the-inhibition mode of action set up.Anyone interested in a gain-of-function protein-protein interaction target? You’d better not be. Targets that have no small molecule binding site at all are going to be a lot harder, too, naturally – you can think about an antibody in those cases, but you’re still going to be limited to what an antibody can do for you (which is basically to block a protein surface). All this ties back in to knowing the human biology: which knob you’re trying to turn and which direction you’re trying to turn it.

3. You need insight into biomarkers, and these need to be as human-relevant as possible. Some diseases have it easier here – diabetes, for example, But others are quite difficult, and you have to be careful not to be misled. Plenge says (accurately) that “Unfortunately, many pharmacodynamic biomarkers measure biological states that are irrelevant to human disease“, and you’d better not just end up measuring something because it’s the thing that you can measure. He also notes that epidemiology is a powerful tool, but by itself it says nothing about causality. Combining it with human genetic studies (“Nature’s randomized clinical trial”, as he puts it) gives you a much better shot at understanding what you should be looking for in blood or tissue during your own clinical trial, the one that you’re going to be paying for.

4. Finally, when you get to that trial, you need one that’s as small, fast, and meaningful as possible to test proof-of-concept. “Well, sure”, you’ll say, but taking this to its logical conclusion means that there are some diseases that you should strongly consider not even considering (see below). This also means that you need to be able to pick your patients very carefully to find the ones that are most likely to show a response (which ties in with the points above about already having connections to human biology). If you can do that, and if you have a real biomarker that you can trust, you’re in very good shape – well, as good as it gets in the clinic, anyway. The further away you get from these ideals, the more you’re rolling the dice.

OK, there are the principles. One of the good things about this paper, though, is that it honestly discusses the limitations of all these ideas:

First and foremost, there is an underlying assumption that we have sufficient data from humans to enable the discovery of new therapeutic targets and biomarkers. Validation of this assumption requires an ecosystem to define which sources of human data establish causality; members of the ecosystem must then work systematically toward building such databases that are accessible to all. For example, there is no single resource that enables systematic identification of human genetic variants linked to clinical outcomes in large patient populations (>10 million people) in a setting suitable for recall. Similarly, there is no large population with detailed molecular longitudinal profiling to identify novel biomarkers. It is encouraging, however, that many efforts are under way to generate these human databases.

Other problems include that you may not be able to get any decent “experiments of nature” by mining human genetic diversity, or even if you do, that they may well not tell you how much to modulate your proposed target. There’s also the problem that clinical trials technologies and designs may not (or not yet) allow for the sort of data collection and biomarkers that you’d like. Even with these complications, I’d say that these criteria are definitely worth aiming for. But even if you have all of them going for you, you can still easily fail in the clinic. Note also that even though many infectious diseases score high by these standards, targets for them can be hard to come by – those projects tend to have high preclinical failure rates, which aren’t addressed here.

One implication of these rules isn’t spelled out in the paper, but seems inescapable: this means that there are some diseases that you just don’t work on. Alzheimer’s is the first that comes to mind. The human biology of the disease is still a matter of intense debate; the potential targets likewise. And as for a short, high-powered proof of concept trial, well, we’re so far away from running one that it makes you want to weep. No, Alzheimer’s scores very high in the “unmet medical need” category, but you’ll note that that’s not one of the things that we’re scoring here. It’s up to you, in a separate exercise, to decide if a given disease or target is worth working on in that sense, but do note that huge medical need is totally orthogonal (at best) to any calculation of chances for success. Bernard Munos has said this for some time now: given the state of Alzheimer’s research, drug companies should probably abandon the field until we understand it better. That’s not going to be popular if you just come out and say it in so many words, but a number of companies have implicitly taken just that course of action by not working on the disease.

The biggest problem I can see with these rules is that it’s very, very hard to meet all of them at the same time. Something’s going to come up short, and judgment calls are going to have to be made about which of those are deal breakers and which aren’t. I’d say that lack of any human biology connection is a deal-breaker, for example, while lack of a really good fast-readout biomarker is just a sign that you’re going to be spending a lot more time and money in the clinic than you want to (not that that’s not a big consideration in itself). But I think that overall, Plenge is correct, that the closer you come to these ideals, the better off you’re going to be. They’re something to shoot for.

50 comments on “Rules for Modern Drug Development”

  1. Diver dude says:

    Speaking as a clinical pharmacologist who helped design small, fast, and meaningful proof-of-concept studies for 20 years, I’d add one more rule – abide by the results of that study. If the study does not work, halt the project. Do not proceed directly into hail-Mary P2b programs wasting time, money and morale on a lost cause.

  2. Chrispy says:

    If you play this de-risking game long enough you end up working on antibodies instead of small-molecule drugs. Antibodies have a built-in specificity and PK and flat-out predictability that small molecules can’t match. (The suicidality of the anti-IL17R antibody Brodalumab was particularly surprising for this reason — if that had been a small molecule there would have been no surprise.)

    This is one of the many reasons chemists in pharma have been having such a tough time of things.

    1. Barry says:

      the PK of antibodies is only acceptable if you are content to discard all potential intracellular drug targets, and aren’t interested in oral dosing. That means you’re discarding the OTC market before you’ve even begun.

  3. Kelvin says:

    Rubbish paper, when you think about it. All it says is that you’re more lokely to succeed when you pretty much already know you’re going to succeed. Which means you’re either working on something that is not really that new, or else it is blindingly obvious and everyone else is working on it. This is exactly what innovation *isn’t*, and lies at the heart of Pharma’s failure. If you want to innovate, then you are going to have to do something different, and be prepared to fail more often, but fail cheaper.

    1. Derek Lowe says:

      How do you fail cheaper when you’re doing something that’s so different?

      1. Kelvin says:

        Identify the biggest risks/assumptions and find a creative way to test them as early and as cost effectively as possible. Coming up with an original idea is only half the story, but finding a cheap and innovative way to test it is where the real ingenuity is required.

        1. Mol Biologist says:

          Mostly important scientific/drugs discoveries and inventions happened by accident. Rules are meant to be broken since the discovery is coming from an acceptance of a contradiction. For example human genetic diversity vs rare mutations rate is the contradiction. IMO the failure coming from ignorance and not an acceptance the fact that mutations are not primary reason for majority of human diseases including cancer and CVD.
          The biggest problem I can see is a decision-making responsibility If the study does not work to halt the project. Yes, you can do it cheaper if stop the project early. Or by Kevin’s words “This is exactly what innovation *isn’t*, and lies at the heart of Pharma’s failure”.

        2. c says:

          Wanted: Chemists interested in multidisciplinary career paths.

          Desired traits:
          -An interest in outrageously innovative efficiency.
          -Dedication to the team.
          -Willingness to volunteer in human tox studies…
          -Chemistry or whatever.

          Please fwd CVs to CostEffectiveCheapAndInnovative Technologies LLC.

          1. Kelvin says:

            The company is fake. Perhaps if pharma companies did seek such innovative multidisciplinary people rather than more cogs to run the same old broken R&D model, they might actually find a better way.

          2. anony the mous says:

            Agreed, with a clarification.
            I’d say interdisciplinary, not multidisciplinary.
            I mean, the questions we are trying to answer require more than just different perspectives coming to a team. They need a level of creativity that tends to occur when colleagues are not afraid of walking out of their comfort zones and wonder into uncharted territories.

            Understanding Human Biology is not just a task for biologists, and that is part of the issue stopping us from making faster progress.

          3. waffler says:

            Kelvin “Perhaps if pharma companies did seek such innovative multidisciplinary people rather than more cogs to run the same old broken R&D model, they might actually find a better way”

            I find this really funny. I don’t know where you work, but you aren’t my boss’s boss’s boss, by any chance, are you? He specialises in this kind of verbiage and is always encouraging everyone to innovate and ideate with elaborate metaphors. Completely out of touch with reality, of course. Anyway, I can assure you that part of the problem with pharma is that is it’s increasingly stuffed with such people who would rather pontificate endlessly about why the model’s broken instead of getting on and doing some real work aimed at discovering drugs.

    2. ScientistSailor says:

      Yours is a straw man argument. He is saying that these factors lead to improved chances for success, but in no way guarantee it. Even if you tick all the boxes, you still have to find a molecule that does what you want in a safe manner. This leaves plenty of room for innovation.

      1. Kelvin says:

        Who said anything about *guaranteeing* success? I was merely pointing out the clear inverse correlation between probability of success (degree of certainty based on existing knowledge) and novelty (innovation based on new/future knowledge). Which is pretty obvious when you think about it!

  4. Phil says:

    This is probably a dumb question:

    Rather than “abandon the field,” would drug companies be smarter to fund/collaborate on basic Alzheimer’s research? No one wants the PR debacle of pulling out completely, but it seems like it would be cheaper to set up an institute to focus on it rather than keep taking long shots into the clinic.

    1. kriggy says:

      Collaborate with who? WIth each other? And who would then get the patent right for the compound?
      With academia? Im sure there is something like that

      1. Phil says:

        Munos’ point is that we don’t understand the biology well enough to get to the compound stage. It would have to be pre-competitive, pure biology. That’s why I said basic science.

      2. cookingwithsolvents says:

        The semiconductor industry has many models that work out very, very well to do just that. Everything from the semiconductor research corporation to other mechanisms. Pool your funds through an ip-sharing organization and get to work. Pharma and the chemical industry just don’t seem to be interested in the benefits of these models.

        1. zero says:

          That’s because the industry shares the results of this research. New breakthroughs in physics, process technology and equipment are shared across participating foundries / fabricators while new breakthroughs in layout, etc. are shared among the big-name vendors. Shared in the sense of prearranged cross-licensing, so certainly there is money changing hands.
          Semiconductors are a poor comparison to pharma. If Intel or AMD comes up with a novel way to address memory (for example) they can license that tech to other companies in order to profit without harming revenues; in fact, standardization helps them as it improves the chances of support for that tech being built into major operating systems. If Pfizer comes up with a novel way to kill malaria parasites then they either use it themselves with patent exclusivity or license it and create a competitor in the market for that compound/technique.

  5. Eric says:

    From the article: “Targets should be selected on the basis of a deep understanding of causal human biology, not on the basis of imperfect and notoriously inaccurate animal model data, whether causal or correlative.”

    This sounds like a good approach on the face of it, but I wonder whether there is really any evidence to support it. Understanding disease biology for complicated diseases like osteoporosis, diabetes, CVD, or alzheimers is an enormous hurdle. If that’s the barrier to entry, there will be few new projects initiated. If the pharmaceutical industry waits 15-20 years until we have a deep understanding of Alzheimer’s disease etiology, and then another 5-10 years to get something to market, will the end result really be better? It seems likely that it could lead to better efficiency (fewer failures / dollar spent), but it seems unlikely that we would get treatments any earlier. I’m also skeptical that it would substantially increase the number of new approvals/year which I assume is the ultimate goal for society.

    1. Kelvin says:

      Fully agree – discovering a new drug does NOT depend on understanding the underlying mechanism. This is a reductionist approach and it is failing more and more often with diminishing returns as we dig deeper and deeper into more complex biological systems (down the rabbit hole). Our greatest mistake is in believing that we must understand anything in order to discover something, but every molecule in our body has evolved to work just fine without any understanding of some grand designer; and there is no reason why the same principles can’t be applied to drug discovery. Iterative exploration and evolution always beats intelligent design (and hubris) in the long term.

      1. Phil says:

        Kelvin, I fully agree that it’s not a requirement to understand mechanism before developing a drug. But the practical question is whether (allegedly) understanding the mechanism increases your odds of success or not. Hubris is assuming the understanding we have is 100% complete and then expecting it to translate 100% into success. But imperfect information (treated appropriately as imperfect) is still useful.

        Evolution accomplished a lot, but it accomplished it on a time-scale that is useful for species, not for individuals. As we set out to build our own watches, we should probably use what sight our blind watchmaker gave us.

        1. John Kent says:

          This is a great point. There is a large dollop of reductionist arrogance in presuming one can understand any target enough to ensure success. Probably more importantly and less obvious to a chemist, by example, is the role of circuits and networks in endocrine and CNS disorders, inherently difficult to test until one enters human trials, where upstream and downstream impact of a “target” on patient symptoms may not be predicted by animal models.

  6. Nick K says:

    Had these rules been followed during the golden era (1830’s to 1990’s

    Had these rules been applied during the golden age (1950’s to 1980’s) we would never have found a single useful drug.

    1. Andrew says:

      Sure we would have, by sheer luck, the same way we did in the real world.

      1. Nick K says:

        Not so. By definition, if a company enforces such rules on its discovery programs, serendipity and happy accidents become difficult or impossible.

  7. Steve says:

    At least all the Alzheimers drug failures will tell us about what Alzheimers is not. A few more billion dollar failures and we may finally narrow it down.

  8. SP says:

    Anyone interested in a gain-of-function protein-protein interaction target?
    Chemical inducers of dimerization?
    As far as Alzheimers, at least there are some “experiments of nature” with protective and risk alleles.

  9. steve (not the previous Steve with a capital S!) says:

    Well, let’s see. How about the first-line drug for diabetes? We still don’t know how metformin works. Statins? When approved they were thought to act through inhibition of HMG CoA reductase and SREBP but it’s now known that they also act through PPARgamma, Rho/ROCK, Rac, P2X7, etc. The idea that you need to know everything about mechanism is one of the great myths of large pharma. The fact is that there probably aren’t any diseases or meds where we really fully understand mechanism. How many effective meds have been left on pharma shelves because of the false notion that you have to have a fully validated mechanism?

    1. Phil says:

      This crossed my mind as well, but the paper is about increasing your chances of success. If you start with a (possibly erroneous) understanding of causal biology, do you believe your chances are better or worse than if you have no information about MOA? I’m sure the intuitive answer is you’re better off knowing (or thinking you know) the mechanism, but I honestly don’t know whether the data would bear that out.

      1. Kelvin says:

        So here’s a provocative question: Do we really want to maximize probability of success??

        Surely 50% is the *ideal* probability of success for a single trial or experiment, since you can add the most value by eliminating uncertainty. After all, there’s no point investing in a trial where the odds are 0%, or even 100%, because you have nothing to learn.

        1. Phil says:

          Hah. I recognize your comment from another thread we are both on.

          I think your model is missing a key variable, money. Not all experiments are equally costly, and for that matter, not all answers are equally valuable. Taking this into account, an experiment with a 1% or 99% chance of success could be more valuable than a coin flip (let’s say, we flip a penny and you keep it if it’s heads, I keep it if it’s tails).

          1. Kelvin says:

            True, my question assumes all other factors are equal, including cost and potential upside.

        2. Josh says:

          Kelvin, I would claim the answer to your question depends on your specific objectives and phase of discovery and development.

          If your question is simply “is my compound safe and efficacious?” then you would want a low probability of failure in a trial as that reduces costs. Assuming your prediction is correct, financial costs would be reduced by a high probability of success. Additionally, ethical costs are reduced in that your experiments would be less likely to lead to a negative outcome for trial participants.

          However, if you are seeking to learn how to identify compounds which do something desirable (modulate a target, are non-toxic, etc.), then running experiments that are 50% likely to succeed (or high uncertainty) are indeed the best as they are going to yield the most information allowing you to more accurately predict which compounds have desirable characteristics.

          The idea of identifying informative experiments in extremely complex experimental spaces (i.e. drug discovery) is currently being tackled using active machine learning methods. By using these methods, very accurate predictive models can be built very quickly by iteratively running experiments. These methods have been demonstrated to work well in lead optimization campaigns. As it turns out, running experiments to learn more about a process (high uncertainty experiments) then trying to find candidates (high certainty experiments) can actually be much more efficient than focusing exclusively on the search for candidates (high certainty experiments). This is primarily because the high certainty predictions from the active machine learning process tend to be much more accurate than those generated using other selection strategies less focused on finding new information.

          Full disclosure: I am the CSO of a company called Quantitative Medicine ( and we offer a service allowing researchers to use this approach.

  10. Not A Chemist says:

    Using 3-year rolling averages for late-stage pipeline assets, estimates of peak sales have decreased by nearly 50% over the past 5 years, from $692 million (during the period from 2010 to 2012) to $451 million (2013 to 2015)

    If I understand this correctly … I know you live to discover new drugs, but this is awesome. New drugs are becoming less and less profitable. Less and less useful. As a human being I have to celebrate the fact that you add less and less value compared to the folks back in the 80s who developed the new drugs of the mid 90s that have now rolled off patent. Not trying to be mean. I don’t care how low-hanging the fruit was. If you can’t beat it then billions of people are better off.

    The article is in a sense simplistic, saying that the best outcome will occur when

    You know what the target is
    You know you can modulate the target
    You can measure the impact of modulating the target
    You run a fail-fast trial that determines if that impact is good

    Is that a reasonable standard against which to measure your phase I trial candidate? I know some of you think it is too strict. I am pretty sure 4 is easier if you have 1 to 3. I guess 3 is the most important, but should you roll the dice on 3 if you don’t have confidence on 1 or 2?

    Should the chemists or the MBAs make this decision? That’s not a trivial question.

    (And I totally get the first comment about no Hail-Marys! :))

  11. DoctorOcto says:

    Interesting that you mentioned human genetic diversity. This approach could lead to development of treatments for people with specific genetic profiles, while alternate profiles may remain uncured. There is a potential ethical issue with this kind genetic discrimination.

  12. Bernard Munos says:

    There are actually some “experiments of nature” with Alzheimer’s that might shed light on the etiology of the disease, and would be worth investigating. The ApoE4 allele is widely seen as a risk-factor, while ApoE2 appears to be neuroprotective. Why is that? There is not much difference between the two.

    Here is another one: for all the evidence that ties ApoE4 to Alzheimer’s, Nigerian blacks have the highest observed frequency of ApoE4 in the world, but the prevalence of Alzheimer’s in that population is quite low. Again, why? At the other end of the spectrum, the inhabitants of the Colombian village of Yarumal have a high frequency of a different mutation–the Paisa mutation–that dooms them to early-onset Alzheimer’s ( What differentiates Nigerian ApoE4 homozygotes from Caucasian ApoE4 homozygotes and from Paisa carriers?

    Researching this would be much cheaper then running large-scale phase III trials aimed at targets that have failed multiple times, based on the hope that “this time it’s going to work”. We have thrown over 350 drug candidates at Alzheimer’s (list available upon request). More than 210 have failed, and, of those still under consideration, none has caused much excitement so far. Throwing compounds at diseases we don’t fully understand is generally not a bad strategy. It has given us many valuable drugs. But after failing 350+ times, it’s time to step back and embrace a different strategy, such as looking at experiments of nature.

    As a final head-scratcher, two recent papers put a different spin on all that. A group at Harvard has shown that the 18 SNPs most commonly associated with Alzheimer’s do not have enough explanatory power to identify patients at risk. However, if the analysis is broadened to include 16,123 SNPs, a statistically significant relationship can be established (Mormino et al., doi: 10.1212/WNL.0000000000002922). Another group at UCLA/Buck reports some spectacular reversal in AD pathogenesis from using a customized “systems approach” that involves many components beside pills. It’s a small study that must be duplicated, but it’s unusual enough to warrant attention. (

    1. Kelvin says:

      “However, if the analysis is broadened to include 16,123 SNPs, a statistically significant relationship can be established.”

      Did they correct the p-value threshold for multiple hypothesis testing? After all, if you test enough *potential* correlations at a fixed p-value of 5%, then 5% of them will be deemed significant by chance alone. How many did they really test (not just report on) before they found a correlation?

      1. steve says:

        Bernard, I think your post is actually the perfect rebuttal to Plenge. The amyloid theory as well as the tau theory fit most of his criteria. It made perfect sense to attack these targets; problem was, we didn’t know that they wouldn’t work until we did the trials. It shows why a mechanism-based approach is not the end all and be all of pharmaceutical development. Sometimes your favorite mechanism doesn’t result in an effective drug; sometimes you have an effective drug but it doesn’t work according to the mechanism you think it does. Human physiology is a multi-layered network of interactions and permutations at one node will have ramifications at all the other nodes regardless of how much target engagement studies you do. That’s why statins have pleiotrophic effects and don’t operate by the simple HMG CoA/SREBP axis that they were designed to hit. The bottom line is that the body is complex and there is not a single approach to drug design that is guaranteed to work no matter how “disciplined” the approach. Drug developers need to be open to serendipity, to observation and to the fact that some drugs may work quite well but we probably will never know exactly how.

        1. steve says:

          BTW, take a look at anesthetics. They probably work through multiple mechanisms but the truth is that we have no idea how they exert their anesthesia. There is no way that Plenge’s rules would apply here and if pharma companies followed them we’d never have the entire class of compounds.

        2. Kelvin says:

          Correct, and at the end of the day patients and regulators only care that a drug works, not how it works, except for academic curiosity. So we should maximize the quality and efficiency of phenotypic screening in the most relevant models to find what works as quickly and cost effectively as possible, and only bother with the mechanistic stuff if and when the drug is approved and you feel like chucking a few million dollars into finding out why.

          1. Phil says:

            steve, Kelvin – I mostly agree with you, but I think you take it too far. Reductionism is not the be all end all, nor is phenotypic screening. MOA is more than academic curiosity, it is valuable information that should help determine which experiments to run first. Like any other scientific endeavor, you use the data you have, come up with a tenable hypothesis, and test it.

            Even if your vision is blurry, you’re going to get your darts closer to the target with your eyes open than with them shut.

            And anyway, the best phenotypic screen still isn’t going to translate 100% either. The only phenotypic screen with 100% predictive validity is an efficacy study in humans. In the good old days, it seems to have been easier to get to human trials to test the hypothesis for real (mechanism aside, if it were developed today, aspirin would never get past preclinical in rats and dogs), and so we have all these old drugs that work despite us not knowing why. But that’s just not the way things work anymore.

          2. Kelvin says:

            Phil, I’m more worried by hallucinations than blurry vision – being blind is better than seeing things that aren’t there at all, because at least you can feel your way around and you’re not being misled into a false sense of confidence.

    2. Mol Biologist says:

      Well defined contradiction. What differentiates Nigerian ApoE4 homozygotes from Caucasian ApoE4 homozygotes and from Paisa carriers? One more how supercentenarians have a lower incidence of cardiovascular disease and stroke than controls? And one of them carries a pathogenic variant associated with arrhythmogenic right ventricular cardiomyopathy (ARVC), which had little or no effect on his/her, health as this person lived over 110 years.
      IMO this is right direction. Respectively, what is actual weight of mutations vs genomics background? It depends, because some people are lucky enough to ignore deadly mutations with
      Evolutionary advantages in their genome which allow them do not count on it. I cannot find the reference right now but I saw it early that apo E4 carriers have “floating membranes” and altered passive and active transport through it. So, in case of Nigerian ApoE4 homozygotes may have something very unique in their microbiome gut brain axis and this keep them off Alzheimer disease. But I am not sure that this little thing in their gut will help people from Western word, since genomics background could be very different.
      There is another good example that confirmed the gut brain axis since apoe4 carriers might be to avoid alcohol entirely 🙂

    3. bank says:


      With respect to APOE alleles and AD in African populations, there are two documented factors worth considering. The first is that there are additional APOE variants common in the African population that are not common elsewhere, for example Arg145Cys. There are others variants common in East Africa. The second is that there is now a confirmed interaction between APOE4 and malaria. Together, these could confound a direct comparison of the effects of variation in the APOE locus on AD in the African population with its effects in non-African populations.

  13. MoBio says:

    Interesting ideas though in terms of psychiatric medications they were discovered before any hint of MOA, genetics and so on was known.

    Antidepressants, antipsychotics, anxiolytics and lithium all discovered essentially by accident.

  14. antibody advocate says:


    An edit is warranted to feature 2:

    “…but you’re still going to be limited to what an antibody can do for you (which is basically to block a protein surface).”

    See this patent application for a contrary example:

    I’d also consider BiTE’s as antibody derivatives that do more than “block a protein surface.”

  15. MoBio says:

    In looking over the paper I note DRD2 identified retrospectively in schizophrenia as a risk factor. Although this is, perhaps, true a close examination of the paper ( ) shows 108 (!) loci (not genes) which are implicated. Although it is true that a locus encoding DRD2 is found there is evidence from the paper that a DRD2 variant (coding or non-coding) is involved as one of the 108 loci. Additionally there is no data on the directionality of the variant (e.g. does it enhance or decrease DRD2 levels/function).

    Another issue relates to GPCRs in particular. In many cases GPCRs do not show haploinsufficiency (in other words if one allele is dysfunctional there is no net effect on physiology). Only in rare cases in which there is complete deletion or constitutive activity will genetic be informative.

  16. Bernard Munos says:

    @ Steve and Mol Biologist
    My take on Plenge’s argument is that hypotheses should be inferred from the study of nature’s experiments rather than animal models or other methods disconnected from human biology. In the case of the Nigerian vs. Caucasian ApoE4 homozygotes, the hypothesis that ApoE4 has a causal role in AD pathogenesis does not hold. So, we should discard it, or at least hold off on new trials until we understand what role, if any, ApoE4 plays in Alzheimer’s etiology. I know of an extended family where the ApoE4 allele is common (along with ApoE3) and and yet its members have lived routinely through their 80s and 90s without a single case of Alzheimer’s or MCI having ever been observed. Given the epidemiological evidence that documents an increased risk for ApoE4 carriers, one may infer that there are other factor(s) yet to be discovered that mitigate its impact. Understanding what they are would seem to be a faster way to a disease-modifying therapy than running large-scale phase III trials that rest on a flawed hypothesis.

    1. steve says:

      Agreed; the only problem is that no one knew that the theory was flawed until the Ph3 clinical trials were conducted.

  17. Ron Richardson says:

    Important to note that PD-1 came mostly from mouse model data.
    Turning everything into a well defined orphan disease probably isn’t a financially viable model for the industry as a whole. Some small companies will make a return for their investors, but you can’t run the entire drug discovery apparatus and healthcare system on $250,000 therapies with 2000 patients.

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