I am about to go
to a meeting in Europe where one of the topics of discussion will be where
Europe should spend its money on antibiotic discovery research. Of course,
geographically – in Europe – sorry Americans.
But what kinds of discovery research should they support with their
Euros? I’ve had this conversation so many times now that I am starting to sound
like a broken record even to myself.
Every time this topic is raised (with academicians) the first two words out
of their mouths are “New” and “Targets.” In theory – this is a great idea. If the antibiotic hits something entirely new
and different than what is hit by existing antibiotics, at least the resistant
strains that exist today won’t be resistant (at least mostly) to the new product – until they
become resistant that is. And every time I hear these arguments, I get a little less tactful in my response. But who cares? I’m retired – right? I can say what I want (mostly) – right?
My thoughts run
as follows.
Every
pharmaceutical company in the world already investigated a very large number of
new targets during the 1990s and early 2000s. Just read David Payne’s wonderful
exposition of GSK’s
efforts in this regard (assuming you have a subscription to Nature or you want
to pay). We certainly went through the same trauma at Wyeth and so did Schering
and many many others. Unfortunately,
much of the billions of pages of resulting data were never published because
the results were, almost 100%, negative! And those of you in the academic world
know how hard it is to publish negative data. There were some interesting
scientific observations that were published based on this research – but little
of the kind of data noted by David Payne and colleagues made it to press. So
what will the academic community bring to this table?
First on my wish
list would be a way to understand how we can make small molecules enter
Gram-negative cells and avoid efflux. This
is a basic science research effort that can be separated to a large extent from
drug discovery per se. Hans Moser has
already published some fascinating work on this topic and additional
research is already being funded to some extent by IMI.
Then, even if we
identify a novel target – what makes us think we can find a drug that will work
against that target? Academic
researchers in general are not trained to carry out drug discovery research.
And when they try to enter the area without adequate training, the results are
not good.
So – what do I
say to people who ask me if they should spend money on research into novel
targets for antibacterial drug discovery in academia?
1.
First –
get academics trained in antibiotic discovery research. They must understand many aspects of
translational research that they currently have not even considered. This
includes everything from biophysical properties of small molecules to PK/PD to
toxicology to chemical manufacturing. This seems like the highest priority to me.
2.
Get
people to think about new approaches to existing antibiotic classes. This is less risky and might well provide
more bang for the buck. How about some
additional B-lactamase inhibitors targeting the class D carbapenemases.
Lots of people (Merck and AstraZeneca among others) have worked on this
class of inhibitors known fondly as DABCO.
Why not focus efforts on a set of enzymes where there is high medical
need? Are other companies working on
this? Of course. Have they gotten anywhere? – not to the stage
of clinical trials at least according to clinicaltrials.gov.
3.
Encourage
research on known targets using new approaches.
Look at all the binding sites in ribosomes that have not yet been
explored.
4.
Finally,
if you plan to spend taxpayer money on research in novel antibacterial targets,
require researchers to provide a chemically tractable ligand that binds the
target and gets into bacterial cells and avoids efflux before you throw too
much money at the project. Seed money OK.
Small projects with high risk – OK.
But that’s it.
For more on this
topic, my blog contains a number of articles on writing grants for antibiotic
discovery (1,
2,
3,
4,
5). I have also previously discussed
the issue of training for academics in antibiotic drug discovery.
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