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Academia (vs. Industry)

What Translational Research Should Academia Do?

We’ve talked quite a bit around here about academic (and nonindustrial) drug discovery, but those posts have mostly divided into two parts. There’s the early-stage discovery work that really gets done in some places, and then there’s the proposal for the big push into translational research by the NIH. That, broadly defined, is (a) the process of turning an interesting idea into a real drug target, or (b) turning an interesting compound into a real drug. One of the things that the recent survey of academic centers made clear, I’d say, is that the latter kind of work is hardly being done at all outside of industry. The former is a bit more common, but still suffers from the general academic bias: walking away too soon in order to move on to the next interesting thing. Both these translational processes involve a lot of laborious detail work, of the kind that does not mint fresh PhDs nor energize the post-docs.
But if there’s funding to do it, it’ll get done in some fashion, and we can expect to see a lot of people trying their hand at these things. Many universities are all for it, too, since they imagine that there will be some lucrative technology transfers waiting at the end of the process. (One of the remarkable things about the drug industry is how many people outside it see it as the place to get rich).
I had an e-mail from Jonathan Gitlin on this subject, who asks the question: if academia is going to do these things, what should they be doing to keep the money from being wasted? It’s definitely worth thinking about, since there are so many drains for the money to go spiraling down. Mind you, most money spent on these things is (in the most immediate sense) wasted, since most ideas for drug targets turn out to be mistaken, and most compounds turn out not to be drugs. No matter what, we’re going to have to be braced for that – even strong improvements in both those percentages would still leave us with what (to people with fresh eyes) would seem horrific failure rates.
And what I’d really like is for people to avoid the “translational research fallacy“, as I’ve called it. That’s the (seemingly pervasive) idea that there are just all sorts of great ideas for new drugs and new targets just gathering dust on university shelves, waiting for some big drug company to get around to noticing them. That, unfortunately, does not seem to be true, but it’s a tempting idea, and I worry that people are going to be unable to resist chasing after it.
But that said, where would be the best place for the academic money to go? I have a few nominees. If we’re breaking things down by therapeutic area, one of the most intractable and underserved is central nervous system disease. I note that there’s already talk of a funding crisis in this area (although that article is more focused on Europe). It may come as a surprise to people outside medical research, but we still have very little concrete knowledge of what goes on in the brain during depression, schizophrenia, and other illnesses. That, unfortunately, is not for lack of trying. Looked at from the other end, we know vastly more than we used to, but it’s still nowhere near enough.
If we’re looking at general translational platforms and ideas, then I would suggest trying to come up with solid small-organism models for phenotypic screening. A good phenotypic screen, where you run compounds past a living system to see which ones give you the effects you want, can be a wonderful thing, since it doesn’t depend on you having to unravel all the biochemistry behind a disease process. (It can, in fact, reveal biochemistry that you never knew existed). But good screens of this type are rare, outside of the infectious disease area, and are tricky to validate. Everyone would love to have more of them – and if an academic lab can come up with one, then those folks can naturally have first crack at screening a compound collection past them.
More suggestions welcome in the comments – it looks like this is going to happen, so perhaps we can at least seed this newly plowed field with something that we’d like to see when it sprouts.

26 comments on “What Translational Research Should Academia Do?”

  1. johnnyboy says:

    “one of the most intractable and underserved is central nervous system disease. (…) we still have very little concrete knowledge of what goes on in the brain during depression, schizophrenia, and other illnesses.”
    Agreed, but research into those disease mechanisms doesn’t sound like translational research to me – much more like basic research, such as is already being done in academic labs all over.
    As for suggestions, here’s a crazy idea. Five years ago, I would have said, like most readers of your blog, that the NIH getting into early drug discovery and development (what I understand they mean as ‘translational research) was a stupid idea. for all the reasons already discussed, which boil down to academia not being geared for this type of work, while pharma is. But in 2011, with the biggest pharma companies slashing research budgets and dropping entire therapeutic areas, I think this may no longer be so stupid. What I’d like to see is the NIH not focussing on a few specific drug targets or therapeutic areas, which by mere probability is doomed to failure, but rather gearing up to do all the assays necessary for drug candidate development. In my field (safety), that means all the necessary assays to get to FIM (animal efficacy models, safety pharm, even tox path). The know-how involved in these is not specific of one drug, it can be applied to any candidate, so it’s not like putting all your efforts into a couple of specific candidates and failing after years of efforts and untold millions. Their translational research center could therefore function as a kind of CRO for potential candidates coming from university labs.
    But if you’re looking for specific therapeutic areas that are underserved, I think one of the most neglected one (and getting worse) is antibiotics. Combine the ongoing emergence of multi-drug resistant bacteria with population explosion, failing economies, and on-going divestment of pharma from the field, and it’s a recipe for disaster. Since the NIH’s mission as a governmental organization is to further the public good, this to me should be one of their primary focuses (before more intractable, age-related problems like cancer and AD).

  2. Luigi says:

    You seem to have overlooked – as many have – the prototypic CNS phenotypic screen – the Irwin test that was used for many years with great success – that was how MK801 was discovered almost a decade before it was identified as an NMDA modulator. This has been refined into the SmartCube by Psychogenics and produced some interesting data. Unfortunately we seem totally enamored with transgenic models and we all know that the amyloid models used in AD research are models of amyloid deposition NOT AD!

  3. lt says:

    “I think one of the most neglected one (and getting worse) is antibiotics.”
    Have to agree there: it wouldn’t be funny at all if in the near future we could print/grow replacement organs to order only to have the recipient die from an infection with pre-penicillin odds…
    I’d also like to see more organism-in-a-microwell development with lot’s of different fluorescently tagged proteins etc in all sorts of cell types you can look at under a good microscope with lots of channels for detection. Although the idea of heavily gene-engineered vaguely fetuslike and faintly glowing cell assemblies made from human stock in kept in vast robotic racks in dark, humid rooms seems likely to raise protest…

  4. student says:

    Translational research is not a good academic project. Faculty often go into research because of research freedom. The sad fact, however, is that we’re all money whores now, to some degree or another, because of the funding climate. There will always be people willing to do what the money guys tell them to do. This does not mean that it’s a good idea. SARs/Pk studies–these are boring studies, not something good to train grad students/postdocs, which is one of the prime reasons the government funds academic research to begin with. IN contrast, these are good studies for the preponderance of PhD gradueates, who prefer not to think of new research directions, and are perfectly happy cooking up a whole batch of side chains, etc.

  5. weirdo says:

    It ain’t sexy, but a huge, seemingly intractable problem is predictive toxicology. Which is, unfortunately, almost completely ignored in academia.
    And I mean that all the way back. Too many molecules fail in 5-day tolerance, or 4-week tox, or 6-month tox (pre-clinically), let alone in Phase 2, Phase 3.
    We need better tools to avoid side effects earlier.

  6. g says:

    Translational drug discovery needs a focused commitment. It doesn’t work to change your target of interest every couple of years. It also doesn’t work to find hits with HTS, do some quick in vitro experiments and small animal experiments, publish a paper, and then go looking for something else that you can publish. There nees to be incentives to create a long-term commitment, both for the academics and the centers.
    Here is an interesting article talking about the productivity and limitations of academic drug discovery:
    Nat Rev Drug Discov. 2011 Jun;10(6):409-10.
    US academic drug discovery.
    Frye S, Crosby M, Edwards T, Juliano R.

  7. Innovorich says:

    One of the biggest problems that pharma has had is all following the same targets and then all failing together when they turned out not to be so well validated targets.
    NIH confound this problem by continually funding the same academic studies on the same targets. What the industry needs is for NIH to be filling the pipe with novel validated targets. Maybe something like Arch2POCM is the only thing that will ever get this going properly if the NIH isn’t willing to take the required risks.
    And on the tox thing – maybe more information could be gained in more high throughput, information rich, and predictive systems like zebrafish screening were applied more regularly.

  8. get real says:

    #7: I often look at this site with some entertainment and often amusement. Can’t resist the reference to zebrafish. Tell me, how does one relate anything about target pathways, effect on physiology routinely, routes of administration, PK, metabolism, potential for drug interactions, monitoring for potential acute toxic effects such as cardio events, in zebrafish? One needs to get real.
    I once worked in an organization where one part was pressing hard to use this as a general screening model several years ago, until it was recognized that the model was, simply stated, not at all practical or supportable for use in drug discovery or development.
    This is one of those glaring demonstrations alluded to by Derek where some folks with focus on academic science are not ready to be given funding for pursuit of real, practical efforts toward usable human drugs. They simply don’t know the right directions to move the work into a practical application from an idealized vision.

  9. RKN says:

    Translational research isn’t only about finding new drugs or new molecular targets. It also involves “translating” the rapidly increasing deluge of high-dimensional information (e.g. genomic and proteomic) into knowledge to, for example, better stratify patient populations. This remains a big problem for clinicians. For example, how to treat an early stage cancer, normally or more aggressively?
    Which existing drugs to use and in what combination (or not) is a legitimate goal of translation research. In other words, maybe we have enough drugs, but what we don’t know is how a particular patient will respond. I just read a piece in the Atlantic Monthly that mentioned a study which evidently found that 85% of new drugs that make it to market are of “little or no benefit to patients.” If true, I wonder if this is not a problem with the efficacy of the drug per se, but rather a problem of not having enough knowledge to predict which dose of the drug, and/or which combination of other drugs, will give a particular patient a good outcome.

  10. William B Swift says:

    Slightly off-topic, but is there some sort of database of candidates that have been tried by various companies and found not to work? I mean very early stage testing, before the candidates got to clinical trials. That could prevent a lot of unnecessary repetition as well as a source of data for statistical analysis of toxicological reactions of specific and classes of molecules.

  11. MoMo says:

    Derek, Are you serious about neuroPharm research? Multiple institutes abound in just about every country with state-of-the-art facilities and big money invested. Go down to Janelia Farm in VA sometime and see the billion-dollar facility built there.
    But is there an equal amount being spent in antibiotics or infectious diseases? No way!
    You are disappointing me with your groupthink like the big boys in Pharma. Once America wakes up from its pharma-over-prescribed-neurodrug-induced stupor the alert masses will put these execs in cages to be led through the streets to be poked at with sharp sticks for their chemical crimes against the un-suspecting public.
    Meanwhile E. coli will shut down kidneys worldwide, MRSA strains will eat our skin and bones while VRE ravages the rest of our organs.
    And translational research will be deemed a “fad” akin to the last several pharmascience has had to endure.
    But good of you to post your picture. That way I won’t jab you if I see you in a cage.

  12. lynn says:

    Being an antibiotics person – I’m all for increased funding for academic research in the field. But what is not needed is just another HTS approach to your favorite target. That’s the current NIH PA out there now. What is needed is an understanding of how to get chemicals into bacteria [where the targets are], especially gram negative bacteria, and how to avoid efflux. We don’t know how to make chemicals that do that. And the chemical libraries we have are not good matches for antibacterials physicochemically. So, I’d fund collaborative research between microbiologists and chemists on figuring out how to make good antibacterials [and I don’t mean “natural product-like” -those big ol’ things are great for gram positives – not so much for gram negatives]. My dream is a rule of 5 [or whatever] for gram negatives – even though all my chemist friends are skeptical.

  13. Dr. Manhattan says:

    the “translational research fallacy”…..That’s the (seemingly pervasive) idea that there are just all sorts of great ideas for new drugs and new targets just gathering dust on university shelves, waiting for some big drug company to get around to noticing them.
    And, indeed, Pfizer appears to be falling into that tarpit with their latest moves to establish small translational groups around big academic centers. I have grave doubts that will amount to anything of real utility.
    Also, MoMo has a very good point with regard to Bacterial Infectious Diseases (full disclosure: I have worked in that area for many years). Modern Medicine’s foundation is the ability to do all sorts of wonderful procedures (hip replacement, invasive surgery, cancer chemotherapy) that absolutely rely on a capable way to control infection. That capability is eroding fast.

  14. johnnyboy says:

    @10: all serious companies would of course keep such databases in various forms, and all would obviously be confidential. Such information is quite important for the management of drug R&D, and is obviously scrutinized very closely.
    But you appear to have the misconception that a drug that is “pre-clinical trial” is in “very early stage”, which is quite far from the truth. It will take several years of intense preclinical research before a molecule goes into a phase 1 clinical trial. Along the way there are many “go/no-go” points (these are not necessary standardized between diffent companies, or even between different therapeutic areas of a same company). So companies have data for the percentage of drugs that pass or fail each of these decision points.

  15. lynn says:

    @10 Wm B Swift
    Would that there were such a database! There’s lots of literature, meeting presentations, patents on early stage programs – but hardly any information out there on what stopped their further development. Industry hasn’t published [much] on it. Of course, academics don’t publish much on their failures either. However, I completely agree that knowledge of what the failures were and why would be extremely useful. I believe all of us industry scientists would be happy if all our failures were published. At least then, people might see that lack of products in the clinical pipeline is not due to lack of trying!

  16. MoMo says:

    You are wise and thorough in your description! Tell those chemists you know they need to grow a spine and get cracking!
    But there have been great microbiologists who have said the same thing you have and you must have known some of them. One of the more dynamic and influential of them wanted to start a large Janelia Farm-type research facility just for antibiotics, but death intervened. Now the Pharma industry is slowly coming around but even then all you hear is 3 years! 3 years to proof-of-principle or you are out!
    Antibiotics are like a fine wine, they take time and loving effort to create. And they save lives, not just treat symptoms like NeuroDrugs.
    Pharma only has patience for Mad Dog.

  17. gippgig says:

    One good focus would be prevention. There is far too much effort spent on curing diseases compared with preventing them in the first place. As the saying goes, an ounce of prevention is worth a pound of cure.
    The human body isn’t designed to maximize long-term health. There isn’t much that can be done about that, but the body’s controls aren’t set at the optimum values for long-term health either and something can be done about that. Activating stress defenses (antioxidants, DNA repair systems, protein quality control, etc.), turning down the speed control (i.e., activating AMPK), etc. show great promise but the data are limited, preliminary, or contradictory. Determining the most effective ways to optimize long-term health would probably have incredible benefits.
    A related issue is determining which nutritional supplements are actually helpful.
    Another issue is developing new & better vaccines.

  18. Anonymous says:

    I think this would have to be done with academics who have some experience working in industry. I had very little understanding of how industry works when I got out of grad school, and I doubt profs are much better.

  19. mad says:

    The real problem is loyalty. Research is a long term investment. Companies don’t give job security and long term incentives to researchers. So why would they expect researchers to care about the long term health of the company? If immediate gratification is how you measure researchers they will find something to gratify you no matter what hidden (undocumented) problems there may be…Scientists are starting to think like hard core business men…grab what I can and get out…reap and move on…This is why there is so much garbage out there.

  20. Innovorich says:

    #8:” I often look at this site with some entertainment and often amusement. Can’t resist the reference to zebrafish. Tell me, how does one relate anything about target pathways, effect on physiology routinely, routes of administration, PK, metabolism, potential for drug interactions, monitoring for potential acute toxic effects such as cardio events, in zebrafish? One needs to get real.”
    Okay I’m not an academic or a zebrafish biologist but actually all the things you just mentioned are doable and assessible in zebrafish.

  21. buddyroo says:

    Regarding central nervous system diseases, here is a review of 3 new books out talking about how ineffective current options are:
    Basically, anti-depressants are “extra strength placebos” and anti-psychotics could be doing more harm than good. Definitely room for much improvement here.

  22. weirdo says:

    Um, really? I’m not nearly as negative on zebrafish as #8, but:
    PK, (human metabolism), routes of administration, cardio events.
    I would trust nothing from zebrafish as being applicable to humans in these areas, that you claim are “doable and assessible in zebrafish”. Either positive or negative. The data just aint’ there.

  23. Innovorich says:

    Well okay that’s fair – PK, (human metabolism), routes of administration – no not really.
    But there’s lots of data on cardiac safety in zebrafish. Labs have image recognition software to monitor QT elongation caused by hERG blockers and can observe many other similar cardiac events. There’s a bit more info here:
    Like I say, I’m not an expert and I didn’t mean to hijack this thread with the comment on zebrafish!
    What do people think about Arch2POCM as a concept:
    (this is a lot more relevant to Derek’s post, perhaps)

  24. get real says:

    20: “Like I say, I’m not an expert and I didn’t mean to hijack this thread with the comment on zebrafish!”
    This is “EXACTLY” the type of problem encountered when folks without certain relavent experience or proper analysis or expertise try to weigh into a topic in this type of blog as if they are credible. If so wise, experienced, visionary…..why are you not actually doing it and putting the world of Pharma R&D to shame? Yet, it IS appreciated that you acknowledge the problem here with your lack of expertise, even though belatedly, and back away from more.
    However, even though is sounds almost cartoonish, the idea of using razerfish carries more weight to the overall topic around the potential role of academics than might appear on superficial view. Many academic lab directors will not, are not interested in, cannot afford, would not be funded, to pursue the longer term, more tedious, less breaking-edge, less innovative, but necessary activities needed in moving “new concepts” into a more practical, applicable realm. Let alone, go through all the hoops, jumps, leaps, bounds, regulatory demonstations, expertise review (some self-proclaimed), safety evaluations, proof of principals and concepts, toward getting some novel, conceptual “read-out” as a truly validate “biomarker” of disease, individualized treatment, drug preference, potential efficacy or failure. USE RAZERFISH FOR R&D, an academic derived concept from over 10 years ago, is exactly this type of topic, and fits perfectly into the overall demonstration of why most US based academic research labs are not interested, emotionally or psychologically fit or focussed, time-line accepting, or really interested in getting to the end of such a purpose. Most would prefer to dream, stay in the world of truly valuable education and (sometimes) new and (even rarely) innovative research, yet still filled with elements of make-believe on global impact. A few folks are truly interested, and are indeed visionary while also being demonstrated as accomplished (not just self-preclaimed)….but in it all, remarkably very few.

  25. Innovorich says:

    Well lots of industry pharma labs/companies are using Zebrafish – this isn’t just an academic thing of no practical value. I mentioned more as a “have people seen this” than with any intention to spend reams of this blog teaching people about it. I think perhaps you actually know less on the subject than i do but are insisting on spouting your opinion in a much angrier, as-if-more-credible, way.

  26. get real says:

    25: I’ll stand by my statements. My challenge to you is to point to what areas zebrafish have actually made substantivie contributions to new drug discovery or development over the last 10 years, and then review after another 10 years. My future is that, predictably, the outcome will not have substantively changed than the immediate past.

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