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What to do when you know the project you're working on is going to fail

  1. May 17, 2012 #1
    So basically we work on small molecules for anti-cancer therapy in our lab (one aspect). The problem is that the molecules we're working on look promising in-vitro, but have absolutely horrendous issues with things like water solubility, being too lipophilic, and more likely than not, will be easily metabolized and excreted before it will even get into plasma. The only problem is that everyone in the lab seems to want to ignore the writing on the wall, just so they can continue to do research or not admit that what they're doing is going to fail. Nobody wants to listen, and they continue to crank out horribly designed compound after compound that, yes, each have interesting biological activity, but stand no chance of getting out of test tubes and into an organism. Not being water soluble is a huge liability, how exactly are we supposed to give our compounds to a living organism? Injection will be extremely difficult, and if you start trying to use excipients like cyclodextrins to help forumulate our compounds into something that can be given IV, you run the risk of running through a field of landmines with IP issues. Not to mention IV drugs cost much more to administer than something orally administered.

    If we try to give our stuff orally, the compound is going to have very poor bioavailability it looks like and it is also looking like it is going to be easily chewed up by CYP enzymes (not to mention massive doses that will need to be given that would probably cost $200,000 per dose).

    What would you do in this situation? Speak up, point out the huge gaping flaws in our research, and become enemy no. 1 in lab and also have your PI find you annoying, or just shut up and design the best in vitro compounds ever that in all likelihood will 0 translational use and write lower impact research?
    Last edited: May 17, 2012
  2. jcsd
  3. May 17, 2012 #2
    This is my advice :smile:
  4. May 17, 2012 #3
    write a paper, grab your degree and move on with your life.

    if given the choice between nothing publishable and something not necessarily bad, not ideal, but publishable, I'm taking the 2nd all the time. that is because in a job, if you tell your manager "yo boss, I think your idea's whack, so I didn't do it by the deadline" you get booted while if you did a bad job based on your manager's idea, he gets the blame instead of you. it's a useful self preservation strategy.

    a question about your actual research: ever try some sort of drug delivery system with viruses or block copolymers, and just letting the drug diffuse out after endocytosis from the tumor cells absorb the drug delivery thing (whether it be a polymer nanoparticle or a virus)? this is of course nontrivial but just something to think about.
  5. May 17, 2012 #4
    The essence of research is failure.

    Keep publishing papers saying "this is what we did and this is what we found." Once in a blue moon, you'll hit some other research group that manages to work around your problems, or you might find that what you are researching is totally useless for your original purpose, but it happens that it's useful for something that is totally different (i.e. the drug that we are testing turns out to be useless for hypertension because it has this side-effect of causing people to grow hair..... Wait a minute.)

    Even publishing a paper saying "this is totally useless" is useful.
  6. May 17, 2012 #5
    A drug delivery system with viruses will almost not be feasible translationally. Any viral delivery system is going to face almost insurmountable scrutiny from the FDA, and to date, if I'm not mistaken, there have been very, very few biologics or combinations approved (probably 0 for viral delivery systems). Polymers have the same problem. If you make 1 change to a polymer system, you have to have it approved by the FDA. You aren't allowed to tweak around with it on the fly once you are in the clinic. We have used polymer nanoparticles that were made from materials already approved by the FDA, however the loading capacity is awful. It works, but loading is terrible, and you would still need a huge dose to see efficacy in a living organism.
  7. May 17, 2012 #6


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    I have the feeling that this happens suprisingly often in science: Groups doing research that is obviously pointless, and never mentioning the huge heap of deal-breakers it involves to anyone outside their immediate field (i.e., to people who don't see it by themselves). Some such research finds its way into Science and Nature. In academia the mere fact that something will never work is not a commonly accepted reason to not do it anyway.

    I would recommend to publish things, get your degree, and then get out of the lab and do something more fulfilling the next time. If you want, you can try to make a game out of it: What is the most ridiculous study we can still publish? And who knows, you might still stumble across something useful along the way (I firmly believe that actually *searching* for something useful is a better approach than hoping for luck, but if you are cornered, you can just as well make the best of it...).
  8. May 17, 2012 #7
    haha, sorry, my field right now isn't drug delivery.

    if you want something marketable, then I'm afraid that it's going to be almost impossible for you to publish anything on time. pharmaceutical companies take 10 or more years to do the work you are doing right now; do you want to graduate in 10 or more years?

    and just like the guy above said, the graduate school is a useful time for learning some theory, experimental techniques and getting to see cutting edge technology at work (at least in materials... I get to see the inside of a cleanroom, how many people get to see THAT?).

    as for employability, well, hopefully you've picked up programming, electronics, chemical synthesis, etc. skills that are useful.
  9. May 17, 2012 #8


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    It is important to recognize the limitations of what you're working on though. Maybe it's time you had a discussion with your PI to see how he or she sees these issues. Inevitably you'll end up at a conference somewhere in a hall filled with hundreds of people all looking at you when someone will ask this very question.

    As others have pointed out, it's not necessarily a bad thing that your compounds will have issues in vivo. Maybe they will only ever lead to a means of curing cancer in cellular models. But that just might give other investigators a better model to work with. It might allow them to answer questions like what happens when certain gene is expressed or not expressed as tumour cells begin to die off at various rates, or a means of instigating a bystander effects where killing one cell instigates the a factor that triggers apoptosis in others nearby.
  10. May 17, 2012 #9
    This is exactly my point of view. Why not ask these questions now ourselves? Someone along the way is going to do it, better us than them. Why waste millions of grant dollars (and tons of PI hours trying to get those grants) on research that has very low translational probability? It's only a matter of time before someone starts becoming critical of just years and years and years of in vitro work with no tangible results.
  11. May 17, 2012 #10
    There's a reason for that. If it was likely that the research would be immediately useful then some private company would pay money to get it done. If the research is being done in a non-profit university, that means that it's extremely unlikely to result in any sort of product that is immediately profitable. So most academic research is doomed to failure, because anything that isn't doomed would be done by someone else.

    In the business world, projects get cancelled very quickly the moment it looks likely that its useless. They is often not a good thing.

    Actually, I don't. The reason that academic research exists is that probably 95% of projects go nowhere. It's the tiny fraction that totally change the world that's worth the effort.

    One other thing. Something to remember is that if your PI gets a grant to research X, then they are legally required to research X. They may think that researching X is stupid and useless, but they don't have any choice in the matter. One could argue that resources would be better spend researching Y rather than X, but that's a semi-political decision that's not only above your pay grade, but it's likely to be above the pay grade of your PI.

    In fact funding agencies will often refuse to allocating grant money to research promising approach Y but rather insist on researching "useless" approach X, in the theory that Y should be researched by the people at major megacorp.
  12. May 17, 2012 #11
    You can ask the question. There are answers.

    I think the basic question is whether or not there is a specific issue with your laboratory, or if you are running into issues that are general with any sort of science research, at which point moving to another lab is not going to help things.

    Because anything that has high translational probability is going to have no shortage of funding from for-profit entities.

    Sure, at which point funding gets cut, redirected toward something else, and life goes on. Also, the questions that get asked are very deep ones. Not merely why should we spend money on approach X on cancer research, but rather whether spending money on cancer research is worthwhile at all?

    One thing that worries me about these sorts of debates is that more often than not, the choice isn't between spending $X on something useful and $X on something useless. The choice is between spending $X on something and spending nothing at all. Something that might be useful is that if you think that spending $X on this approach is useless, what do you have as an alternative. What do you think your laboratory should be spending its effort on?
  13. May 17, 2012 #12
    If people scream enough, then the FDA can change it's rules. Also the FDA doesn't have worldwide jurisdiction, so if the FDA doesn't approve anything innovative, then some other country might. Same with IP issues. There are countries that have adopted a "screw IP" when it comes to biotech research.

    Also sometimes you *want* the issue to be resolved about your pay grade. There is a reason why the FDA is so restrictive with new research, and frankly the ethical issues involved are so nasty, that I'm glad that I'm not making these sorts of decisions. But if you come up with research that says "we could do X to save lives, but rules X, Y, and Z won't let us do it" that's an interesting fact that you can hand off to the politicians, lobbyists, and lawyers and let them work out.

    Few questions:

    1) Do you think the world would be better off if your lab got shut down? That's an important question because I've found that the millisecond you mention "waste" and "science", there will be a ton of politicians out with knives ready to shut things down. It's *never* lets spend less money on X we can spend more money on Y. It's always, lets cut X. Period. There are times when cutting X (period) is a good thing. If your lab was doing ethically questionable things. But I don't get the sense that this is the situation.

    2) What are the terms of your funding? If you have a mandate to study X, then you must study X.

    3) Are the limitations scientific or are they political/legal? If someone asks for several billion dollars to develop warp engines that travel faster than light, then that's scientifically stupid, and I feel comfortable in killing that. If the limitations are political, legal, or sociological and not a matter of science, that's a totally different issue. The laws of physics aren't going to change, but laws of Congress can and will. One thing that colors my experience is that I've spent a lot of time around lobbyists, and they are professionals at getting laws and regulations changed.
    Last edited: May 17, 2012
  14. May 18, 2012 #13


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    Any kind of thorough post-mortem for all people including people on the project, and people potentially interested in the project (i.e. other people in your field) will definitely get a lot out of you completing the research and saying what the faults were and what the take-away has been (even if this means you don't produce results that are 'positive') because it means that anyone who reads this won't make the same mistake.
  15. May 18, 2012 #14
  16. May 18, 2012 #15


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    @OP, any "failure" of a scientific project is a possible advance in knowledge. We can't advance science only by "proving" ideas are right - that's not the way things happen, IRL. We can advance our knowledge by showing that some ideas really don't work out well. Negative results are not wasted effort or time - they are critical to our understanding.
  17. May 18, 2012 #16
    At the same time you still have to have a rationally designed approach to what you are doing. Which path offers least resistance-- designing a molecule that is actually going to work in vivo first and sorting out the biology from there, or creating any old thing that you want in order to achieve X biological result even though what you're making will be extremely difficult to get working in an actual organism? I'm sure cyanide and all sorts of heavy metals can kill cancer beautifully in in vitro experiments, but how exactly can you make those work in an organism? That's essentially what we're doing.
  18. May 18, 2012 #17


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    You seens to have a basic misunderstanding of what "research" is about.

    If you want to work on projects that have a clear path from start to finish and are expected to deliver something workable on time and within budget, give up "research" and go to whatever is the biochem equivalent of "engineering".
  19. May 18, 2012 #18
    That's the thing, I'm in biomedical engineering.
  20. May 18, 2012 #19
    yeah biomedical engineering's like that.

    the biggest contributors to lifespan expansions was sanitation, vaccines and antibiotics that suppressed infectious diseases which hit fast and hard. Chronic diseases such as cancer are much harder to fight, much more costly to fight, and make much lower contributions to lifespan expansion or even quality of life increases.

    However, chronic diseases are also theoretically interesting to try and solve, and what's more, they make big bucks for the pharmaceutical company. That's why there's research being done on them. Just keep in mind that even if someone made a nanobot that swam through your bloodstream and could instantly identify and destroy cancer cells, it'd be 1.) millions of dollars to deploy and 2.) would probably extend life for just a few years.
  21. May 18, 2012 #20
    My facetious answer - well, that's the problem. You're trying to do synthetic/medicinal chemistry in amongst engineers. Of course they're not going to understand. ;)

    You mention that this is one aspect of the lab's research. How does this work fit in with the rest of the research being conducted? You don't have to answer that here, but you might want to think it through and see if it might be viewed more charitably.

    On a "my memory is like a steel trap" note - I recall you inquiring a little while ago about 19F MRI and, subsequently, boron-containing molecules. I'm speculating here, but if your lab has interests in medical imaging (not an unusual situation for a BME lab), there's definitely a reasonable interest in preparing novel molecules for imaging purposes. The emphasis might be more on new ways to probe biological systems and less on developing a viable drug candidate.
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