FX125L is a fascinating molecule. A first-in-class anti-inflammatory agent, targeting a newly discovered pathway promoting the resolution of chronic inflammation, it holds exceptional promise as a first line treatment option in a number of major disease areas, including asthma, COPD and rheumatoid arthritis.
As Boehringer Ingelheim announce the acquisition of the FX125L from Funxional Therapeutics, a Cambridge-based privately-held biotech company founded by DrugBaron in 2005, the story of the discovery and early development of this drug product candidate illustrates some important lessons for drug discovery in the 21st Century – whether in a virtual biotech or a multinational pharma company.
The most important characteristics of FX125L are its intriguing new target and its ideal pharmaceutical properties. Both depended on a fair slice of luck, but the way in which we loaded the dice in our favour could be applied much more widely.
Finding a first-in-class therapeutic candidate for a blockbuster indication is no trivial exercise. The process of drugging a new target has been industrialized to such an extent inside global pharma companies that the most exciting new discoveries have been tested as drug targets (and usually thrown in the bin) long before an independent drug discoverer even learns about them.
Small companies, then, are usually left using their agility to develop improved variants of late-stage clinical candidates to fill the pipelines of the fast-followers, or else solving the conundrum of the best indication to treat with any given class of drug product candidates. Discovering and exploiting a wholly new area of biology is typically out of reach.
But what if the normal process of discovery were turned on its head? Instead of discovering a pathway and then drugging it, what about discovering a drug and then identifying the pathway it targets?
That is the principle behind functional screening, where molecules are selected on the basis of a particular functional property rather than for interaction with a particular molecular target. Typically, the functional property is a complex cellular process that in turn depends on many different inputs and outputs any or all of which could modulate the observed function. Our reliance on such a functional screen to discover FX125L led to the adoption of the name: Funxional Therapeutics.
Inspired by the growing interest in chemokines as “address labels” in the immune system during the early 1990s, as well as the difficulties in identifying useful chemokine inhibitors using conventional molecular screening approaches, we established a screen for inhibitors of chemokine-induced leukocyte migration. Critically, this work was carried out in an academic environment, in the Departments of Biochemistry and Medicine at Cambridge University – critical because we were able to spend two or three years fully understanding the intricacies of our screening assay before embarking on a drug discovery project. It would never have been possible to invest so much time understanding the assay in a commercial environment.
With very limited resources, we did not propose to run the screen with a random compound library – not least because a cell-based functional assay is very susceptible to false positives caused by metabolic inhibitors (as we had discovered during our validation of the assay, even very subtle changes in cell size were sufficient to modulate chemokine-induced migration in a transwell assay). Instead, we used bioinformatics and molecular modeling to design candidate peptides that we expected to bind to chemokine receptors.
The first of these peptides were designed and synthesized in 1996 – a full ten years before Funxional Therapeutics was financed to engage in a “real” drug discovery and development project in this field!
The first lesson, then, is that successful projects need a long incubation period. Really understanding what you are doing cannot be accelerated even with unlimited resources.
The first hit, imaginatively named “Peptide 3”, was published in 1999 and was a low affinity (micromolar range) 12-mer peptide that inhibited migration of a wide range of leukocytes in response to various chemokines, but had no effect on migration induced by other chemoattractants (an important control that rules out ‘false positives’ due to toxicity or effects on cell size).
Micromolar range peptides, even with interesting biological functions, are scarcely even useful as tool compounds in vivo, let alone as drugs. So we set about looking for ways to improve the potency. Hundreds of sequence variants were characterized – many lost activity, defining nicely the pharmacophore, but none showed a significant gain in potency. Intriguingly, the effect of sequence changes altered the potency against all the chemokines tested simultaneously, suggested that the peptides were not binding to chemokine receptors themselves, but to a single unidentified binding site.
Creating a cyclic reverse D analogue of the peptide (effectively turning it upside-down and inside out) was more successful: the resulting analogue, termed NR58-3.14.3, was a low nanomolar inhibitor of chemokine-induced leukocyte migration. Gaining 100-fold or more potency on performing the cyclic reverse D trick was unexpected and unprecedented and was the first of several substantial chunks of good fortune.
The half-life of NR58-3.14.3 in vivo was still short (around 15min plasma half-life in rats), but it was potent enough to allow sufficient exposure to be achieved to test the efficacy in vivo. Over the next five years, labs all around the world demonstrated the extraordinary anti-inflammatory activity of this compound in animal models of acute and chronic inflammation as diverse as asthma, stroke, atherosclerosis, endometriosis, surgical adhesions and graft-versus-host disease. It even inhibited HIV replication.
But NR58-3.14.3 wasn’t really a drug candidate. For start, the compound cost at least $10,000 per gram in raw material costs due to the inclusion of D-isoleucine (isoleucine and threonine are the only 2 of the 20 proteogenic amino acids with a stereocentre in their side chain, creating four enantiomers, and dramatically increasing the cost of the unnatural stereoisomers). Cost per dose was only exacerbated by the short plasma half-life and the need for parenteral administration.
So, in 1999, David Fox (working with Stuart Warren in the Chemistry Department in Cambridge) joined the effort. Using the pharmacophore definition from the peptide series, he set about making non-peptide mimics. Finding small molecules that replicate the biological effects of peptides is no small task – and the fact that within 6 months David Fox had delivered a 5nM compound called NR58,4 owed much to both luck and skill. The skill was David’s guiding principle to make small and simple molecules, rather than large and complex ones – something he called the Exupery Principle of Medicinal Chemistry.
The second lesson is to keep things simple
With a potent non-peptide hit in our hands, the journey from hit to lead and through lead optimization was pretty conventional. The imide ring in NR58,4 was the source of metabolic instability, and conversion to a lactam lengthened the half-life. Selecting a pivoyl tailgroup also proved to be a master-stroke, driven once again by the Exupery Principle. The resulting drug product candidate, FX125L, is less than 200 molecular weight with only two functional groups – yet it is a sub-nanomolar inhibitor of chemokine-induced leukocyte migration with pharmaceutical properties ideal for once daily oral administration in man.
Thanks to David Fox and his Exupery Principle, we ended up not only with a first-in-class compound with exciting biological properties, but also with the potential to be best-in-class. Too often, the product of independent drug discovery projects (that is, projects run outside of major pharma companies – whether in academia or small biotechs) are good enough for proof of principle, but are unlikely to dominate a particular landscape. Finding molecules with optimal ADMET properties is usually a task reserved for the legion chemists of the global players. As a result, it can be a close run decision for a pharma company as to whether they gain anything by buying a programme where they will likely opt to start again with the chemistry.
Building a successful exit for a biotech requires more than pace-setting biology – it needs pharma grade molecules too.
But if the chemistry journey that led us to the FX125L molecule was informative, then the biology story is potentially iconoclastic.
The peptides fed into the initial functional screen were designed to bind to chemokine receptors, a group of about 20 type 1 G-protein coupled receptors (GPCRs), a receptor superfamily that was the target of more than 40% of the registered pharmaceutical developed in the 20th Century. The functional assay itself was designed to find inhibitors of chemokine-induced leukocyte migration. The expectation, therefore, was that we would find chemokine receptor antagonists.
Only we didn’t.
The first sign that things were not going as anticipated came from the peptide SAR work: any change to the peptide structure changed the potency for inhibition of migration in the same way irrespective of the particular chemokine used to stimulate migration. If we had a broad specificity antagonist this would not have been the case – changes in structure would have differentially affected affinity at the different chemokine receptors. Instead we appeared to have a single target.
Eventually we demonstrated to our own satisfaction that our molecules did indeed not bind to the chemokine receptors (proving a negative can be a challenge). So where did they bind?
Five years of searching eventually found the answer – the target (for the original peptides as well as for the non-peptide analogues such as FX125L) was the type 2 somatostatin receptor (sstr2). In one sense, that wasn’t such a surprise – sstr2 is another GPCR very closely related (structurally and in evolutionary terms) to the chemokine receptors. But in another sense, it opened up a new fundamental question: how does binding to sstr2 inhibit chemokine-induced leukocyte migration?
The answer, it seems, is that our molecules are partial agonists at sstr2 – they stimulate signaling that overlaps with the signals generated by the related chemokine receptors (but without the effects of classical sstr2 agonists, such as somatostatin itself, on growth hormone levels or the HPA axis). Our best hypothesis is that the strong, uniform signal from sstr2 “drowns” the directional signal from the chemokine receptors and the cell is effectively blinded to the chemokine gradient.
If that were the end of the story, it would be interesting rather than groundbreaking. Our molecules fortuitously co-opt a related receptor to generate a useful functional outcome. But the real excitement came when we realized this wasn’t luck – nature was already using sstr2 to generate a chronic anti-inflammatory signal. We had drugged a natural pathway we didn’t even know existed!
Drug discovery is like making a top claret: lots of dollars is no substitute for careful creativity and a generous helping of time to gently mature.
There are a whole class of natural peptide ligands for sstr2 that had gone unnoticed – and gone unnoticed for a very subtle reason. The key pharmacophore for binding to sstr2 was not the peptide sequence itself, but a novel post-translational modification. Peptides with a C-terminal lactam group bind to sstr2, and generate an anti-inflammatory signal.
Once you know to look for them, you can find peptides with C-terminal lactam groups (we called them C-terminal lactam peptides or CTLPs) in biological fluids. Funxional has amassed considerable evidence that these CTLPs play an important role in the resolution phase of the inflammatory cycle, and more importantly that deficiency in CTLPs contributes to the establishment of chronic inflammatory pathology.
FX125L, like other somatotaxins, are pharmacological analogues of CTLPs, a novel natural ligand playing a role in the regulation of the immune system.
These findings elevate somatotaxins beyond simply being another promising drug product candidate. Irrespective of the outcome of their later clinical development, they have delivered the first comprehensive demonstration of the power of functional screening. As Donald Rumsfeld said in 2002 “There are also unknown unknowns – the things we do not know that we don’t know” – and he could have been talking about drug discovery.
The third lesson (for life, as well as drug discovery) is to be humble: assume there is more that we don’t know than we do know, and make sure your discovery strategies don’t lock out those “unknown unknowns”
Molecular screening can only yield the answers to known unknowns. Where the entire pathway is hidden from view, it lies almost entirely outside of the current discovery paradigm. But using functional screening you can discover things that you didn’t even know you should be looking for. And once you have found them, you can work from the drug candidate back to the underlying biology, revealing, as in our case, exciting new pathways that herald a step-change in our understanding of important physiological processes such as the resolution of inflammation.
The next phase of development of the somatotaxins rightly lies in the hands of a global pharmaceutical company. They have the resources and the expertise to navigate the next set of challenges – such as locating the best indication, and the best patient population, to benefit from the clinical profile we have identified. But the Funxional Therapeutics story powerfully illustrates that a small number of scientists, working outside the drug discovery mainstream, can – given enough time – generate drug product candidates that are competitive with the output of the biggest pharmaceutical companies. Like making a top claret, lots of dollars is no substitute for careful creativity and a generous helping of time to gently mature.