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

[gravenewworld]

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?

 

[Dickfore]

...just shut up and design the best in vitro compounds ever that in all likelihood will 0 translational use and write [STRIKE]lower impact[/STRIKE] a detailed, and honest research paper.

This is my advice

 

[chill_factor]

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 ideas 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.

 

[twofish-quant]

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?

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.

 

[gravenewworld]

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 ideas 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.

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.

 

[cgk]

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.

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...).

 

[chill_factor]

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.

 

[Choppy]

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.

 

[gravenewworld]

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.

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.

 

[twofish-quant]

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.

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 canceled very quickly the moment it looks likely that its useless. They is often not a good thing.

(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...).

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.

 

[twofish-quant]

This is exactly my point of view. Why not ask these questions now ourselves?

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.

Why waste millions of grant dollars (and tons of PI hours trying to get those grants) on research that has very low translational probability?

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

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.

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?

 

[twofish-quant]

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).

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* let's spend less money on X we can spend more money on Y. It's always, let's 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.

 

[chiro]

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.

 

[QuarkCharmer]

 

[turbo]

@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.

 

[gravenewworld]

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.

 

[AlephZero]

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".

 

[gravenewworld]

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".

That's the thing, I'm in biomedical engineering.

 

[chill_factor]

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.

 

[Mike H]

That's the thing, I'm in biomedical engineering.

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.

 

[twofish-quant]

the biggest contributors to lifespan expansions was sanitation, vaccines and antibiotics that suppressed infectious diseases which hit fast and hard.

And the biggest things that are cutting lifespans in the developed world are lifestyle issues and access to health care. You are probably going to save more lives working as a advertising agent for a gym or as a physical trainer than you are as a cancer researcher.

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.

I think what people are hoping for is some insight into the processes that make our bodies self-destruct after 70 to 80 years. Evolutionarily, it's easy to understand. Once you've passed on your genes and raised the next generation, then you are a burden and so natural selection programs in a self-destruct mechanism. I think the real focus of all this medical research is to figure out a way of either disabling the self-destruct or finding out exactly why it can't be done.

There is a weird connection with quantum mechanics. There's this idea called quantum immortality in which a conscious being always finds themselves in a universe in which they don't die. I've been thinking about what the universe would be like if quantum immortality were true, and one thing that would be very strong evidence for quantum immortality would be if some time in the next forty years someone "magically" discovers a way of dramatically slowing the aging process.

I've promised myself that if "weird stuff happens" and I manage to make it to age 150, I'll do the quantum suicide experiment to see what happens. On the other hand, if I have a "normal death" I think one of the my last thoughts is going to be "I guess we live in Cophenhagen."

This is crazy, but making these sorts of crazy connections is what academic research is all about.

However, chronic diseases are also theoretically interesting to try and solve, and what's more, they make big bucks for the pharmaceutical company.

And there are interesting cognitive bias issues. For example, if you had a relative with a major medical condition, then you'd have a very strong interest in screaming at people to spend millions or billions of dollars for a 0.2 probability of having said relative live an extra six months (or even six weeks). If you have a Congressman show up at the hospital, and they say "sorry, in the interests of the greater good, we aren't going to fund this" then you aren't going to be voting for them.

From a standpoint of utilitarian ethics, this is a bad thing, but I think we are biologically programmed to not be utilitarians under some situations.

 

[twofish-quant]

At the same time you still have to have a rationally designed approach to what you are doing.

Welcome to science. Decisions about what research to do and how to do it are not made "rationally" in the ordinary sense of the word. The fact that people are irrational benefits biotech. In the 1960's people were terrified of the Russians so they were begging physicists to save them from the Russians. Today, people are terrified of dying or worse of dying badly. If you spending several hundred billion dollars on 10000 different things, and you discover one thing that saves me from an angonizing death, I'm not going to care about the 9999 things that went no where.

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?

Not obvious. One issue that my wife runs into in her research is that any time you have to deal with living organisms, things get very complicated, very quickly. Laboratory equipment doesn't sue you and if you end up blowing up a glass beaker, then no one has to tell their relatives. If you want to do anything with live animals (or worse yet people) you are looking at months of arguing with the institutional review board, and once you've agreed to a protocol, you can't change it.

If you really think that the direction of research is wrong, then the thing to do is to get experience, and work your way up to the point where you can set the agenda. Research efforts tend to generate lobbying groups, so it takes a while to change direction.

One bit of advice when dealing with funders. It's a very bad idea to say we shouldn't do X, we should be doing Y. Because that gets translated into "we shouldn't do X." It should be phrased as "we should be doing Y." Also, it's a terrible idea to complain about waste and inefficiency in academic research, because by definition academic research is inherently wasteful and inefficient. Once you open up the discussion to "cutting waste" then what happens is that *everything* gets cut.

 

[twofish-quant]

If I sound unsympathetic to your situation, it's because I'm jealous...

I work in an industrial setting, and the *microsecond* it appears that your project isn't going to contribute to next quarters earnings it will get cut. So I spend a lot of my time trying to (usually unsuccessfully) convince my managers to let me work on "useless" stuff.

The frustrating part is that it doesn't take that long for something useless to become obviously useful (i.e. two years) but people's memories are so short (people only look ahead or behind one quarter) that it doesn't matter.

 

[Number Nine]

Evolutionarily, it's easy to understand. Once you've passed on your genes and raised the next generation, then you are a burden and so natural selection programs in a self-destruct mechanism.

I would imagine that the exact opposite is true; natural selection has nothing at all to say about what happens after you reproduce (how would it say anything?). The problem is that there are no selective pressures to weed out aging related degenerative processes, since reproduction has occurred long before then.

As for the OP: I sincerely doubt that the facts you've described have escaped your PI. The fact is that he's committed himself (legally and financially) to a research program that will not ultimately be successful, but will result in a decent publication or two and will teach us something about the molecules with which you've been working. If you have anything insightful to offer (even if critical), then by all means share with your professor, but be aware that he has enough experience that he's probably aware of the flaws you've pointed out.

 

[twofish-quant]

Since I've had unfortunate experiences with relatives that have had cancer treatments...

It doesn't *seem* like what the OP is doing is useless, and I think he should just keep doing it.

1) I've never gotten the sense from the doctors that getting the drug to the tumor was much of a problem. The doctors are very clever at getting stuff to the tumor, and something that seems to be pretty common is to put a catheter to inject the drugs directly into the tumor, and I've been impressed at how clever they are. So the impression that I've gotten is that once you have something that works, bioavailability is an "easy" problem.

If you got something that is not water soluble then you can mix the drug with a lipidol and then inject it into the artery that is feeding the tumor with a catheter, and then the lipidol not only delivers the chemotherapy, but also blocks off the blood supply. This is something that's already "standard procedure" for certain types of cancer.

If none of this will work, then my impression is that the doctors and surgeons will figure out something that will.

2) Any late stage cancer patient is going to be semi-permanently connected to an IV anyhow. There are getting a half a dozen drugs through an IV. They'll be connected to a bunch of tubes putting stuff in, and another set of tubes taking stuff out.

3) Cost is not an issue if you have insurance. Cancer treatment turns out to be insanely expensive, but someone else is paying the bills. There are some deep public policy, social equity, and ethical issues here, but when I'm visiting someone in the hospital, I'm really not in the mood to think about them.

4) One of the more interesting things from a research standpoint is that it turns out to be difficult to impossible to see from one patient whether the treatment is actually working or not. There are dozens if not hundreds of things happening. Every patient is different, and there is a lot of randomness. If you give a patient a treatment and then suddenly they get better, it could have nothing to do with the treatment or it could be some sort of placebo effect. Conversely, if you give a patient a treatment and they get worse, it could be that the treatment is still effective, because it could be that without the treatment they would have been worse off.

It's really impossible to do research studies with one patient since there are too many things going on. In order to establish effectiveness then you have to do statistics, and even that gets tricky.

There's also a tendency in cancer patients to do "kitchen sink" treatments. If you don't know if something is going to be effective, you give them to the patient unless it's obvious that it will make then worse. This actually causes more ethical issues as cancer drugs improve. The older class of chemotherapy drugs were less often used because they had massive bad side effects and killed quality of life. As drugs improve, there is more pressure to "just medicate if we don't know what's going on" if the drug doesn't have any bad side effects.

If it's a choice between massively invasive surgery and nothing, then it's usually clear that nothing is the better choice, because the surgery itself will do bad things. If it's a choice between feeding someone fish oil or doing nothing, then feed them the fish oil. It won't hurt them, and they may get lucky. Even if it doesn't work, then it's going to be another statistic which is going to be useful for the next set of patients.

5) We are all going to die, and I have this impression that a lot of the medical efforts at dealing with late stage cancer are more important psychologically then medically. Some people have spent all of their life being busy, so the last thing they are going to do when dying is to "go gently into the night".

 

[gravenewworld]

Bioavailability is an "easy" problem? I've read reference after reference where they estimate that almost half of all compounds that are being researched for development end up failing because of poor PK/PD, with bioavailability being a big killer. Even if doctors can come up with a clever trick to deliver a drug directly to a tumor, they still have to be able to deliver it in the first place. How do you deliver something through a needle if it won't dissolve in water? Usually a drug is given through IV only if it is very water soluble (since it won't be able to get through your gut)

It sounds like you are describing chemoembolization. You can't easily use lipidiol direclty for formulation (trademarked). Like I said, once you start using all sorts of excipients you start running into a field of landmines with regards to IP. Academic papers that use formulations that are protected under IP almost never address the IP issue. Cyclodextrin has been around for the past 20 years, yet it is only used as an excipient in only 5 drugs. One of the biggest reason it isn't used more is because it is protected under IP, and IP alone can be a big road block for a drug. If you are talking about chemoembolizaiton, the drug still has to be injected into the tumor first, and then an embolic agent used after (lipidol), it isn't quite a direct formulation with lipiodol. Your compound still has be water soluble for it to be injected.

http://en.wikipedia.org/wiki/Transcatheter_arterial_chemoembolization

If your drug isn't water soluble you can't give it through IV, that's the big liability with the compounds we are making. That means that they'll have to given orally and will have to see first pass metabolism. Just by looking at the structures you can almost double down on your bet that they'll be extensively metabolized by CYP enzymes, will also be PGP efflux substrates, and will therefore have poor half lives (which means ungodly doses would be needed).

Cost is always an issue. If you can develop a drug to be orally taken vs IV, oral is almost always preferred. It costs less to administer, takes up less of physicians' time, and can be given outside of the hospital, not to mention the fact that manufacturing an oral drug is easier. It also saves time for the patient from having to travel constantly to a clinic or hospital for treatment (this is a big deal that is overlooked) . If you manufacture something for IV use, you have to be much more concerned with sterilization since you are going to by pass the body's defense systems. This even adds more to costs. Health care spending is already on an unsustainable path, cost containment is always a good idea, and simply ignoring it because someone else is going to pay only adds to the problem. Even if you have insurance, co-payments can still be extremely high, or completely unaffordable:

http://www.usatoday.com/news/health...owing-burden-the-high-cost-of-care/53271430/1

 

[twofish-quant]

Like I said, once you start using all sorts of excipients you start running into a field of landmines with regards to IP. Academic papers that use formulations that are protected under IP almost never address the IP issue.

And I don't think they should. If scientists start restricting research based on what the lawyers tell them to do, and if it turns out that there isn't a good ethical or social reason for those laws, then I think this is going to be a very bad thing for the world.

In any case, with respect to IP. If we have stupid IP laws, then we need to change the laws, and if you can point to people dying because of laws, then that gives you something that the lobbyists can use to change them.

If we can't change the laws in the US, then I'm all for setting up cancer clinics in some country with less silly laws. If your research is unusable in the United States because of IP reasons, it could be usable somewhere else where people don't care about IP. (Note that I never mentioned that the people I know that are undergoing cancer treatment are in the US.)

It costs less to administer, takes up less of physicians' time, and can be given outside of the hospital, not to mention the fact that manufacturing an oral drug is easier. It also saves time for the patient from having to travel constantly to a clinic or hospital for treatment (this is a big deal that is overlooked) .

And in for late stage cancer patients, this doesn't matter because they are going to be in the hospital anyway. For lots of patients with chemo, then are going to be connected to a glucose IV anyhow because they can't tolerant eating while on chemo.

For late stage cancer patients, convenience and cost to third parties are just not going to be factors. At that stage, you are just buying time and hoping for a miracle.

Health care spending is already on an unsustainable path, cost containment is always a good idea, and simply ignoring it because someone else is going to pay only adds to the problem.

Sure, but I think that if we think about costs first, then that's the tail wagging the dog. If we have drugs that save lives and they are ungodly expensive, then we need more research to reduce costs. If we start off trying to not do research because what we find would be too expensive then we end up with nothing.

Also, if we are talking about cost containment, then this is a useless discussion since the cheapest thing to do is to not treat the patient. Once you've decided to treat, then that's basically a decision that cost does not matter.

Even if you have insurance, co-payments can still be extremely high, or completely unaffordable

Not if you are in a country with a health system that isn't completely broken.

 

[gravenewworld]

And I don't think they should. If scientists start restricting research based on what the lawyers tell them to do, and if it turns out that there isn't a good ethical or social reason for those laws, then I think this is going to be a very bad thing for the world.

In any case, with respect to IP. If we have stupid IP laws, then we need to change the laws, and if you can point to people dying because of laws, then that gives you something that the lobbyists can use to change them.

If we can't change the laws in the US, then I'm all for setting up cancer clinics in some country with less silly laws. If your research is unusable in the United States because of IP reasons, it could be usable somewhere else where people don't care about IP. (Note that I never mentioned that the people I know that are undergoing cancer treatment are in the US.)
And in for late stage cancer patients, this doesn't matter because they are going to be in the hospital anyway. For lots of patients with chemo, then are going to be connected to a glucose IV anyhow because they can't tolerant eating while on chemo.

For late stage cancer patients, convenience and cost to third parties are just not going to be factors. At that stage, you are just buying time and hoping for a miracle.
Sure, but I think that if we think about costs first, then that's the tail wagging the dog. If we have drugs that save lives and they are ungodly expensive, then we need more research to reduce costs. If we start off trying to not do research because what we find would be too expensive then we end up with nothing.

Also, if we are talking about cost containment, then this is a useless discussion since the cheapest thing to do is to not treat the patient. Once you've decided to treat, then that's basically a decision that cost does not matter.
Not if you are in a country with a health system that isn't completely broken.

You're preaching to the choir. I totally agree with most of what you say. It's just the way the world works. For example, we wanted to use liposomes to deliver our drug a few years back, but ran into all sorts of IP issues and can no longer use them for our research (too many licensing issues or whatever).

And the only point I was trying to make wrt to costs is that a well designed molecule has the potential to no only be effective, but also can save a lot of money. The poorer the physio-chemical properties of your molecule, the more it adds to costs and difficulties for efficiency and delivery. It's all a balancing act, but it is generally believed that putting much more effort into optimizing pchem properties like water solubility, # of rotatable bonds, crystal structure, etc. etc. pays off much more than developing whatever drug and spending much more effort on figuring out how to formulate and deliver it.