In drug discovery, what counts is asking the right question

The other day I was having a discussion with a colleague about the drug Velcade which has been used quite successfully to treat multiple myeloma. Velcade is probably the only bestselling drug that has the element boron in it. Boron is a highly reactive element that had never been seen in drugs before. If you had shown the structure of velcade to a chemist fifteen years ago he or she would not have touched it with a fifty-foot pole and instead placed a call to the nearest mental asylum. But that’s not all of it. Velcade jams up the proteasome, the protein machine in our body which is essentially the body’s garbage can. So now you have a drug that looks toxic gumming up the body’s garbage can…which is supposed to get rid of toxic proteins and other junk. Most people would have been forgiven if fifteen years ago they had called velcade not “boronic” but “moronic”.

And yet here we are with the first big drug containing boron which works well; which is prescribed to hundreds of thousands of people suffering from a deadly disease; which has saved thousands of lives.

The velcade story is certainly one of dogged persistence and of countering the prevailing wisdom. But it also illustrates a bigger point which is true of science in general but of drug discovery in particular: In drug discovery, what really matters is asking the right question and finding the right problem. The answers matter of course and we have to find them, but without the right problem having the solution around won’t matter one bit. Boron-containing drugs are not going to work for every target or every ailment. And yet there is one particular target (the proteasome) and one ailment (multiple myeloma) which pose the right question for which an answer exists in the form of a boronic drug.

This theme is repeated in drug discovery all the time, especially regarding paradigms which were thought to be impossible. Nobody thought boron-containing drugs would make it, but it turned out that what we lacked was the right question for which they would provide the answer. Nobody thought that kinase inhibitors would be selective and non-toxic, and yet we found particular chemical structures that worked extremely well for particular protein targets. Nobody thought that a crazy-looking chemical structure like metformin that defied every "rule" of druglike behavior would ever become a drug, and yet metformin is today raking in millions and medicating diabetes patients on a daily basis.

And the beat goes on. As another recent example, covalent drugs were thought to be a huge liability until we discovered unique, non-conserved reactive amino acid residues on important target proteins that could be targeted by such drugs. One of them was even sold for an unprecedented $21 billion a few months ago. Just like covalent drugs and metformin, there are many other paradigms which changed people’s thinking, but the real reason they did so is because someone always thought of the right nail which would benefit from the precise application of that particular hammer.

The other day I was reading an interview with Bob Langer in which he said that the key element in transitioning from a graduate student or postdoc to an independent researcher is to switch from giving the right answers to asking the right questions. He is absolutely right, and it seems to me that this is something that people don’t always realize in drug discovery as well. In fact one might ascribe the several failures of the field over the last few decades to the zeal of those who kept on insisting that they had the right answers (high-throughput screening, combinatorial chemistry, molecular modeling,, structure-based drug design) when what they should have been doing was asking the right questions. It’s not that these tools are useless, it’s that they don’t work unless you have the right problem in front of you that would truly benefit from their application. In fact one factor which distinguishes a good drug discovery scientist from a bad one is the ability to identify the right problem for which a particular approach shows the most promise. One might call it the “pairing up problem”.

Structure-based drug design is a good example of how the pairing-up problem can be fruitfully resolved. Companies like Vertex and Merck pushed structure-based design mightily in the 80s and 90s. The limitations of the approach were quickly (although as some might argue, not quickly enough...) realized, but its application to select targets like carbonic anhydrase and HIV protease in particular yielded some spectacular results. Structure-based design was certainly not a panacea, but it was a solution looking for the right problem. Once the right question was asked the method could be productively used. It continues to improve and wander the wilderness of biological space, looking for apt suitors.

The pairing-up problem is why we always need to recognize the limitations of "rules" about druglike properties and metrics: there are always exceptions falling outside the parameter space of these rules that can be used if we find the right problems for them. The pairing-up problem is also why I am optimistic about many new potential technologies and ideas in drug discovery, from slow-binding inhibitors to nanoparticle drug delivery to genomics. None of these are going to likely revolutionize the field wholesale overnight and many of them have been oversold, but all of them are looking for the right questions for which they would be the right answers. The exciting thing is that the questions are almost certainly there; it’s up to us to ask them.

Image link: Bonus gift of two posts in one! SeeArrOh reminds me that there are some very unhappy bonds and atoms in that stock photo above. As punishment for not noticing this I have decided to spend a day in the lab and make one of those molecules...

Update: I was hounded out of the lab and declared persona non grata for having the unbridled temerity to even step foot in it.