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Derek Lowe The 2002 Model

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Derek Lowe, an Arkansan by birth, got his BA from Hendrix College and his PhD in organic chemistry from Duke before spending time in Germany on a Humboldt Fellowship on his post-doc. He's worked for several major pharmaceutical companies since 1989 on drug discovery projects against schizophrenia, Alzheimer's, diabetes, osteoporosis and other diseases. To contact Derek email him directly: Twitter: Dereklowe

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November 30, 2012

A Broadside Against The Way We Do Things Now

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Posted by Derek

There's a paper out in Drug Discovery Today with the title "Is Poor Research the Cause of Declining Productivity in the Drug Industry? After reviewing the literature on phenotypic versus target-based drug discovery, the author (Frank Sams-Dodd) asks (and has asked before):

The consensus of these studies is that drug discovery based on the target-based approach is less likely to result in an approved drug compared to projects based on the physiological- based approach. However, from a theoretical and scientific perspective, the target-based approach appears sound, so why is it not more successful?

He makes the points that the target-based approach has the advantages of (1) seeming more rational and scientific to its practitioners, especially in light of the advances in molecular biology over the last 25 years, and (2) seeming more rational and scientific to the investors:

". . .it presents drug discovery as a rational, systematic process, where the researcher is in charge and where it is possible to screen thousands of compounds every week. It gives the image of industrialisation of applied medical research. By contrast, the physiology-based approach is based on the screening of compounds in often rather complex systems with a low throughput and without a specific theory on how the drugs should act. In a commercial enterprise with investors and share-holders demanding a fast return on investment it is natural that the drug discovery efforts will drift towards the target-based approach, because it is so much easier to explain the process to others and because it is possible to make nice diagrams of the large numbers of compounds being screened.

This is the "Brute Force bias". And he goes on to another key observation: that this industrialization (or apparent industrialization) meant that there were a number of processes that could be (in theory) optimized. Anyone who's been close to a business degree knows how dear process optimization is to the heart of many management theorists, consultants, and so on. And there's something to that, if you're talking about a defined process like, say, assembling pickup trucks or packaging cat litter. This is where your six-sigma folks come in, your Pareto analysis, your Continuous Improvement people, and all the others. All these things are predicated on the idea that there is a Process out there.

See if this might sound familiar to anyone:

". . .the drug dis- covery paradigm used by the pharmaceutical industry changed from a disease-focus to a process-focus, that is, the implementation and organisation of the drug discovery process. This meant that process-arguments became very important, often to the point where they had priority over scientific considerations, and in many companies it became a requirement that projects could conform to this process to be accepted. Therefore, what started as a very sensible approach to drug discovery ended up becoming the requirement that all drug dis- covery programmes had to conform to this approach – independently of whether or not sufficient information was available to select a good target. This led to dogmatic approaches to drug discovery and a culture developed, where new projects must be presented in a certain manner, that is, the target, mode-of-action, tar- get-validation and screening cascade, and where the clinical manifestation of the disease and the biological basis of the disease at systems-level, that is, the entire organism, were deliberately left out of the process, because of its complexity and variability.

But are we asking too much when we declare that our drugs need to work through single defined targets? Beyond that, are we even asking too much when we declare that we need to understand the details of how they work at all? Many of you will have had such thoughts (and they've been expressed around here as well), but they can tend to sound heretical, especially that second one. But that gets to the real issue, the uncomfortable, foot-shuffling, rather-think-about-something-else question: are we trying to understand things, or are we trying to find drugs?

"False dichotomy!", I can hear people shouting. "We're trying to do both! Understanding how things work is the best way to find drugs!" In the abstract, I agree. But given the amount there is to understand, I think we need to be open to pushing ahead with things that look valuable, even if we're not sure why they do what they do. There were, after all, plenty of drugs discovered in just that fashion. A relentless target-based environment, though, keeps you from finding these things at all.

What it does do, though, is provide vast opportunities for keeping everyone busy. And not just "busy" in the sense of working on trivia, either: working out biological mechanisms is very, very hard, and in no area (despite decades of beavering away) can we say we've reached the end and achieved anything like a complete picture. There are plenty of areas that can and will soak up all the time and effort you can throw at them, and yield precious little in the way of drugs at the end of it. But everyone was working hard, doing good science, and doing what looked like the right thing.

This new paper spends quite a bit of time on the mode-of-action question. It makes the point that understanding the MoA is something that we've imposed on drug discovery, not an intrinsic part of it. I've gotten some funny looks over the years when I've told people that there is no FDA requirement for details of a drug's mechanism. I'm sure it helps, but in the end, it's efficacy and safety that carry the day, and both of those are determined empirically: did the people in the clinical trials get better, or worse?

And as for those times when we do have mode-of-action information, well, here are some fighting words for you:

". . .the ‘evidence’ usually involves schematic drawings and flow-diagrams of receptor complexes involving the target. How- ever, it is almost never understood how changes at the receptor or cellular level affect the phy- siology of the organism or interfere with the actual disease process. Also, interactions between components at the receptor level are known to be exceedingly complex, but a simple set of diagrams and arrows are often accepted as validation for the target and its role in disease treatment even though the true interactions are never understood. What this in real life boils down to is that we for almost all drug discovery programmes only have minimal insight into the mode-of-action of a drug and the biological basis of a disease, meaning that our choices are essentially pure guess-work.

I might add at this point that the emphasis on defined targets and mode of action has been so much a part of drug discovery in recent times that it's convinced many outside observers that target ID is really all there is to it. Finding and defining the molecular target is seen as the key step in the whole process; everything past that is just some minor engineering (and marketing, naturally). That fact that this point of view is a load of fertilizer has not slowed it down much.

I think that if one were to extract a key section from this whole paper, though, this one would be a good candidate:

". . .it is not the target-based approach itself that is flawed, but that the focus has shifted from disease to process. This has given the target-based approach a dogmatic status such that the steps of the validation process are often conducted in a highly ritualised manner without proper scientific analysis and questioning whether the target-based approach is optimal for the project in question.

That's one of those "Don't take this in the wrong way, but. . ." statements, which are, naturally, always going to be taken in just that wrong way. But how many people can deny that there's something to it? Almost no one denies that there's something not quite right, with plenty of room for improvement.

What Sams-Dodd has in mind for improvement is a shift towards looking at diseases, rather than targets or mechanisms. For many people, that's going to be one of those "Speak English, man!" moments, because for them, finding targets is looking at diseases. But that's not necessarily so. We would have to turn some things on their heads a bit, though:

In recent years there have been considerable advances in the use of automated processes for cell-culture work, automated imaging systems for in vivo models and complex cellular systems, among others, and these developments are making it increasingly possible to combine the process-strengths of the target-based approach with the disease-focus of the physiology-based approach, but again these technologies must be adapted to the research question, not the other way around.

One big question is whether the investors funding our work will put up with such a change, or with such an environment even if we did establish it. And that gets back to the discussion of Andrew Lo's securitization idea, the talk around here about private versus public financing, and many other topics. Those I'll reserve for another post. . .

Comments (30) + TrackBacks (0) | Category: Drug Assays | Drug Development | Drug Industry History | Who Discovers and Why


1. Janne on November 30, 2012 9:47 AM writes...

Can you patent a drug without giving a mechanism, though? That should be a somewhat important point, I would guess.

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2. Janne on November 30, 2012 9:49 AM writes...

Can you patent a drug without giving a mechanism, though? That should be a somewhat important point, I would guess.

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3. Chemist with Plan B on November 30, 2012 10:32 AM writes...

Janne--for a composition of matter patent there is no need for a defined mechanism of action. You do need to show that the compound(s) have some utility, but that could be the disease treatment. We've all gotten used to demonstrating utility as "inhibitors of kinase X for the potential treatment of disease Y", but "special molecules for the treatment of disease Y" is equally valid. Demonstrating the utility may be a challenge depending on the disease, but cellular or animal model efficacy would be enough.

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4. Hap on November 30, 2012 10:45 AM writes...

1) I don't think you have to know what a substance does to patent its use in treatment, only that you know that it does what you say.

2) If receiving funding from investors precludes achieving the stated goal for receiving that funding, then perhaps the problem doesn't lie in research.

It seems unreasonable (and unconstructive) that investors expect companies not to take their money to do what they want (rather than what they told investors they would do), yet they expect companies to make money by whatever means, even if those means require repudiating the companies' knowledge, utility, and reason for being to make money in the short term. If I hire someone to make me money designing planes, but instead I decide that in order to make money now, he needs to repair cars, I am not certain why I should think that either the business or my investment is likely to survive. Short-term tactics that destroy the likelihood of long-term survival would seem to be obviously counterproductive, not staples of investment strategy.

If being useful and making money are mutually exclusive, it isn't our concept of utility that needs to change.

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5. rhodum on November 30, 2012 10:46 AM writes...

Can one quantify the success of drug development based upon folk medicine? Although I guess treating erectile dysfunction by looking for objects in the shape of a penis is one approach to target based drug discovery.

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6. road on November 30, 2012 11:26 AM writes...

I think you could still argue that target ID is all there is to it, it's just that true validation of valuable targets often requires good compounds and clinical trials.

The abundance of 'me-too' drugs proves that once a good target is identified, the development of drugs acting at that target is a solvable engineering problem.

The problem is probably that people use terms like "target ID" and "target validation" too loosely.

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7. Perdurabo on November 30, 2012 11:36 AM writes...

The shifting of focus from disease to process seems to be another one of those "confusing the map with the territory" examples

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8. Tjnova on November 30, 2012 11:36 AM writes...

If morphine was unknown as a natural product, do you think a target-based approach would have identified it?

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9. Tjnova on November 30, 2012 11:38 AM writes...

If morphine was unknown as a natural product, do you think a target-based approach would have identified it, or optimized to the morphine structure?

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10. student on November 30, 2012 12:25 PM writes...

The difference between phenotype and in vitro screens comes down to your level of optimism about how much we know about the biology and chemistry of living systems. If you think we know enough to handle the complexities, you may favor the latter approach; if you are a cynic about how much we know, you will favor the former. Derek is clearly a cynic, since he favors phenotype screens, and I agree with him.

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11. Chris on November 30, 2012 12:46 PM writes...

Many good points here and I do believe that we need to be more “humble” in our drug discovery efforts.

Falling short of knowing every single process inside the human body, including differences between individuals, one could argue that there is no such thing as rational drug design. I do think that we need to spend more time looking for compounds that produce a desired effect in cell-based and in vivo models first, rather than focusing on single targets. Focusing on a single target assumes that this target single-handedly governs a pathology in absence of any regulation and redundant signaling, and that is simply not the case usually.

Being more humble and acknowledging that we know very little about human biology may also help clear the disconnect between public perception and the reality of drug discovery. I am always amazed to realize that most people think we have the human body mostly figured out, having to explain that it is quite the opposite and the reason why most drugs fail.

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12. Chrispy on November 30, 2012 1:01 PM writes...

There is an inevitable Catch-22 that validated targets are essentially validated by a drug that hits them. So once a target is truly validated you enter into "me-too" space. I wish I could have all the hours back spent in meetings hand-wringing about unvalidated targets vs. too-late-to-beat-the-competition targets.

One area where you pretty much have to be target-based is in the production of therapeutic antibodies. Yeah, there are a few stories about antibodies made using cancer cells as an immunogen or cloning out antibodies from patients who should have died from a disease they carry. But for the most part you need to decide what you are going to hit.

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13. MoMo on November 30, 2012 1:17 PM writes...

Chris is right on the money here. Screen all compounds in cells then animals with the best models available, and while target directed discovery may be sound in principle, in reality its hit or miss.

But dont kid yourselves. How many diseases are actually "cured" by chemicals? Most drugs outside antibiotics including cancer agents only treat symptoms- ala cardio and neurological drugs.

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14. john on November 30, 2012 1:47 PM writes...

So just throwing this out there as it's something I've thought about but don't necessarily believe.

We train our chemists, biochemists, pharmacologists etc. in classical scientific method which is reductionist in nature.
A thought process that works very well with the idea that one chemical can hit one receptor etc.
The human body is much more complicated than that though, and trying to use this reductionist thinking sometimes breaks down because of the complexity of the body. The scientific method doesn't lend itself to such a complex system so we have to start thinking in a different manner. As a result we see a retraining of scientists in drug discovery, as they have to look at things through a new lens.
I guess what I'm asking is this, is a classically trained organic chemist, who is steeped in the scientific method, really getting the training they need to start thinking about practical drug discovery. Perhaps what we are really training people to do is come up with at best molecular probes for use in cell assays or at best simple model organisms.

I don't know, my mind is wandering on a Friday afternoon and I've been reading some philosophy of science books lately.

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15. Sam on November 30, 2012 2:45 PM writes...

This article clearly brings out the challenges we have in translating basic discoveries related to biological targets into useful therapies. It is unfortunate that distinguished Nobel laureates in their recent Science opinion piece have failed to understand the health care needs and realities in today's world.
(Science 338, 1033 (2012); Joseph L. Goldstein and Michael S. Brown: A Golden Era of Nobel Laureates).

This does not mean basic research is not important.. Its an indispensable source of generating the scientific know-how needed for translational sciences to solve practical problems in discovering life-saving therapies. Both basic and translational sciences should work hand in hand..

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16. MC on November 30, 2012 3:25 PM writes...

I think the problem is not the reductionist approach a priori (it works quite well in science) it is a short cut mentality (e.g. target != target validation != disease modulation) as false promises arising from politics and pseudo (because quarterly)economic pressure (besides the fact that research is not a process).

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17. Hibob on November 30, 2012 4:31 PM writes...

@MC: I think you've just proved the reductionist approach works quite well in critiques of drug R&D as well: " target != target validation != disease modulation" sums up the disconnects quite nicely.

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18. Andy on November 30, 2012 11:28 PM writes...

In oncology biologicals succeed in development to the clinic at twice the success rates of small molecules. It would be easy to argue that the problem with "target-based" small molecules is just that they aren't targeted enough.

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19. Dennis on December 1, 2012 1:45 PM writes...

The challenge with screening in cells or animals is their ability to predict effects in humans. Certainly with a target based approach you can be assured (for the most part) that the same target exists in humans as well as any cells or animals that you construct. I agree that the validity of those targets in preclinical testing compared to humans is fraught with problems and there are lots of cases where a target in humans was a lot less important that your favorite mouse model. However I would say that the animal models for many diseases are deeply flawed. If all we had to do was cure mice with tumors we would have solved cancer a long time ago. Finally, at the end of the day, I still lean towards screening in cells and humans.

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20. Nick K on December 2, 2012 4:26 AM writes...

How would captopril and all the other enzyme inhibitor drugs have been discovered without a mechanistic rationale?

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21. Cellbio on December 2, 2012 12:03 PM writes...

I agree heartily with Dennis that animal models are flawed. I would add that in m opinion they are indeed deeply flawed, I would say so much so as to be totally useless when used as a measure of "efficacy". It is clear that efficacy in models does little to predict clinical success, and further, clinically successful compounds do not always illustrate robust activity in models. It is a complete mystery to me why there continues to be such an over use of animal models.

However, since one needs to validate tox species, it is imperative to show equivalent pharmacology. This is another case where I believe phenotypic screening can be more rigorous that target based approaches. In target programs, showing expression of the target, analyzing homology and demonstrating the compound's activity against the target adds up to validating the tox species. Usually this will include looking at expected pharmacology as well, but then relies on toxicology as the first exploration of broader compound pharmacology, when phenotypic screening does this early, at least the way I think of pheno screening.

The flaw with "assurance" that knowing a target when you step to models and tox is an extension of the fundamental flaw with target mindsets. We presume our ability to draw signal transduction pathways and cellular interactions in neat cartoons accurately captures the reality of the pharmacology, when really it only provides intellectual comfort for our decisions.

On the other hand, phenotypic screening does not presume to know what the compound does through inference of a target's biology, inferences that may not translate well across species, or are built through a hybrid of species, or predominately mouse biology. Phenotypic compounds must then proceed through pre-clinical studies with a pharmacology finger-print, compound does x, y, z, but not a,b, c, a dose response relationship, SAR around those measures, that enables demonstration of activity, demonstration that the "target" is present, and enables determination of therapeutic index. This is more rigorous than most target based compounds, in my experience.

In the end, toxicology is empirical, efficacy is empirical, and it is clear that our paradigm driven belief systems that simplify biology to fit our notions of target validation have not worked well in aggregate, and have enforced a belief system that views a compound's pharmacology as being determined by the intended target of the compound. While one can identify cases where this is largely true, our failures outnumber our successes by such a wide margin that it is more instructive to look at our failures and then one realizes that what we measure in our target based programs is flawed when we are truly exploring the pharmacology of a compound whose activity is certainly not as simple as we presume, and NOT the pharmacology of a target, as we measure only a fraction of what is possible.

In my opinion, target based approaches are flawed in approach (biochemical screens), flawed in focus (e.g. specificity at related targets) and flawed in compound prioritization (animal model efficacy). How many targets have you worked on where KO mice "validated the target", then turn back to show efficacy with a compound. This only validates pharmacological inhibition equates to loss of protein, important, but otherwise quite circular logic. To see this in real life, and I wish I could share the data, screen a collection of target based chemistry, with a high degree od coverage of very similar chemical space, screen it broadly, and then stare at the data and wonder how you can see so much biological variation, variation not evident in the biochemical patterns either.

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22. even lipinski on December 2, 2012 8:17 PM writes...

Even Lipinski weighs in on the topic!
(link in handle)

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23. anonymous on December 3, 2012 7:26 AM writes...


Its the indication that makes the difference. Abs still often fail for oncology and SMs get through at a higher clip than for other indications

Many fewer hurdles through development than other therapeutic areas make onco the go-to area, minimal tox, less restrictive clincial programs etc., endpoints that can be manipulated.

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24. Anon on December 3, 2012 10:47 AM writes...

Anyone who's been close to a business degree knows how dear process optimization is to the heart of many management theorists, consultants, and so on. And there's something to that, if you're talking about a defined process like, say, assembling pickup trucks or packaging cat litter.

"business process optimization" in R&D ... a refuge for scoundrels and boneheads.

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25. exGlaxoid on December 3, 2012 3:18 PM writes...

I think that we will eventually go back to the way they did it years ago. Make many compounds, try to screen them in some cellular or animal models to weed out the toxic ones, or look for best predictors of good DMPK and then go quickly into humans. It worked well for finding anti-histamines, anti-biotics, and many other drugs back in the 1950-1970 era.

The FDA has made doing phase 1 trials so difficult now that no one wants to do them, but I expect that in China, India, or elsewhere they will do this and find new drugs for more things than we can with a million more computer models. Given that there are not that many novel chemicals, we could screen them faster in people than with all of the models, and actually get real data. We can use paid volunteers, willing patients, or even lawyers (some are a half decent model of a human system, just missing a good conscience). But not with the current FDA.

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26. anon on December 3, 2012 9:32 PM writes...

25, there is a lot of truth to what you say, but do you think rolling back safety studies is going to gain traction?

When you look at why most compounds fail, it's not for safety reasons. As a result of the FDA's sometimes unreasonably high bar, many of the compounds are actually safe in people. I think its a tough case to roll back some of that. On the other hand, the real problem is most compounds simply aren't efficacious. Why are so many compounds failing phase 2? They don't do anything.

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27. anon on December 4, 2012 2:37 AM writes...

@6 Keep drinking the kool aid. You don't need target validation to get a me too drug.

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28. r.pal on December 4, 2012 1:30 PM writes...

We are in an the era of metagenome where the number of bacteria and virus cells in our body are 10 time that of the human genome .It is unlikely that we can succeed in drug candidates if we ignore the elephant in the room. As an article in journal Nature Medicine (volume 18, no 4, Page 501,2012) suggested recently “It is time to move from the concept of ‘one drug, one target’ toward ‘smart’ drugs that can simultaneously modulate multiple targets.which may lead to successful treatment of many of these challenging diseases.”

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29. Subrahmanyam Vangala on December 5, 2012 9:30 AM writes...

Here is the problem as I see it.

1) Several Diseases have many over-lapping symptoms with one-another and unless we identify specific biochemical marker or genetic marker we really do not know what disease we are working with. Many diseases still do not have specific markers we can chase after.

2) Many chronic diseases do not occur with one single step process but require multiple cascade of toxic insults before it manifests as a disease (We call them silent killers).

So, in my opinion either for TDD or for PDD we need to have specific disease diagnostic techniques which can be used as theragnostic markers as well. However, many times we try to intercept the disease at a very late stage without understanding the initial steps in the disease process making new drug discovery process very futile for unmet medical needs.

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30. Come On on January 27, 2013 1:25 PM writes...

The elephant in the room really has nothing to do with this. The elephant in the room is that there is no single effort underway to develop any treatment for anything that exists outside of the profit motive. This is the source and root of the shortcomings identified by this and any other discussion of relevant approaches. To be sure I am no enemy of the profit motive, which is the primary motive behind the many advancements in technologies on every front. As Adam Smith once said "It is only for the greed of the butcher that we all eat". And I don't argue the truth of that to great extent. But this does not mean that the profit motive is the only means to the answers we seek. I am typing this response in a window on my Mozilla Firefox browser. Mozilla Firefox is a not-profit, open source browser platform. And it has become the most used, and, in the opinion of many, best web browser in the world. All completely absent the profit motive. How funny that we can develop an open source web browser, superior to all others, through a coordinated volunteer effort, just to waste time watching YouTube videos or checking sports scores. Yet when it comes to creating cures for diseases that compromise the lives and health of all of us, we are constrained to a debate around the finer points of profit driven models. Haven't our own tax dollars funded the academic foundations of many of these technologies through University research. Many assert that selling off these technologies to for-profit ventures robs the taxpayers of something that is effectively theirs. If I work for a widget company who financially supports my development of a new widget, that product becomes their product. However in the drug model, taxpayers often foot the bill for academic research that is then sold to for profit ventures. The taxpayers see no return on this sale, then are forced to pay for treatments that are often subpar in order to afford drug companies the luxury of striking a balance between efficacy and profitability. Profits realized on technologies we funded the first place. Any discussion, even an insightful one like this one, that rests on this model being singular, fixed, and unchangeable, is ultimately inane.
Last year, scientists introduced an online video game modeled around the HIV virus. The game laid out a set of constraints and an ultimate objective presented in a the manner of a 'quest'. In reality the object of the game was to identify an energy pathway to safely exploit and destroy the HIV virus. To the amazement of many, after years of research to this end, the video gaming community took less than 2 months to find the holy grail that had eluded researchers for close to 3 decades. The cost of this discovery was ZERO DOLLARS. Compare that to how much was spent on HIV research for the first 30 years. So when we talk about drug and treatment research in this very limited context of two profit driven models, we fail to even begin to scratch the surface of what options are really available to us. If people want real answers, that lead to real results, and truly advance understanding, then there are far more options available than those presented here. But if all we want is for-profit half-treatments, and all of medical possibility dictated to us from within the confines of for-profit models, then by all means discuss these topics to death. And watch nothing change. Except for the costs to the end user...

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