DrugBaron is fortunate enough to review hundreds of exciting early-stage drug development projects every year, for organizations as diverse as the British Heart Foundation, Wellcome Trust and US National Institutes of Health as well as Index Ventures and Total Medical Ventures.
Such is the competition for resources, that only a small minority win support. Thus will it ever be. But observing so many candidate projects, a pattern has begun to emerge – a pattern that distinguishes the winners from the losers.
The winners have realistically assessed the safety of their approach – and backed up that assessment with data. The majority that miss the cut, by contrast, gloss over the safety issues and rely on theoretical arguments rather than practical demonstration to support the contention they will achieve a viable therapeutic index.
A subtle tweak in the mindset of early stage biomedical researchers aiming to identify new therapeutic candidates would, therefore, deliver enormous benefits. The projects that fail to win support for further development represent a waste of the talent of their inventors, a waste of bandwidth for the industry and a poor return for the money (whether from a charity, government or business) spent in their creation.
Here, then, is DrugBaron’s open letter to those inventors, imploring them to provide a better of assessment of safety for early stage therapeutic candidates:
If you want to see a new therapeutic product brought to the clinic, but you don’t already work for a large pharmaceutical company, then the chances are you will need to convince people like me of the prospects for your invention. Unless you can do so, you will be unlikely to attract the resources that are necessary to get over the early hurdles along the tortuous development path – hurdles that need to be cleared to convince those big pharmaceutical companies to throw the massive weight behind your product candidate that is needed to get it to the clinic.
It seems obvious that the most important component of the early-stage business plan will be convincing data that the new approach actually works; that it successfully treats the pathways and symptoms of a particular disease. Such data likely consists of a mixture of human genetics linking the target with the disease, studies in knockout animals where the target pathway has been disrupted by genetic manipulation and in vitro studies demonstrating that the product candidate does indeed hit the selected target.
Unless your product candidate hits a target that has already been validated in the clinic (when you will face some very different questions about why your follow-on is sufficiently superior to the existing products on the market or in development), this kind of target validation data is essential. For a “first-in-class” product candidate it is a sine qua non for success, and the stronger the dataset the greater the likelihood of a positive review.
But if target validation and efficacy data is the invariant core of the data package assembled around a “first-in-class” invention, what comes next?
Usually, the answer is to take the compound into animal models of human diseases. It is one thing to demonstrate the importance of a pathway, and that your new agent targets that pathway, but another thing altogether to demonstrate a clinically meaningful impact of the intervention in vivo. Such data is often time-consuming and difficult to generate, and depending who the review was for (perhaps a conventional VC firm rather than a government or charitable body) it may also be an essential component of the data package.
Perhaps, but not always, there will be some early data on pharmacokinetics – a simple half-life determination following a single dose administered by various routes in rodents can be very useful. Again, though, such data can be time-consuming and costly to generate principally because of the need to develop a suitable bioanalytical assay for the new agent. Its also less critical because an experienced medicinal chemist or drug developer can make a decent guess as to the likely ADME properties of a compound from the structure lor chemotype alone.
And that, in many cases, is essentially the whole package presented for review. Pages and pages of justification for the importance of the target and the pharmacology of the compound. Some limited demonstration of efficacy in animals perhaps, together with some basic ADME parameters. And two sentences on the likely safety of such an intervention.
Fewer than one in ten of such proposals have any actual data related to the safety of intervening at the proposed target.
It gets worse. Perhaps struggling to raise enough resources to make serious progress, but attracting a small amount of cash to take a tentative step forward, the usual response is to generate more efficacy data, maybe in a different animal model of the same disease, or in model of a different disease altogether, or else in the same model but using different dosing routes or regimens, or perhaps a wider selection of end-points.
All that information is useful, and some of it may even be critical – at some stage in the development programme.
But the key thing to remember, given how difficult it can be to raise cash to spend on a programme, is to ensure that you spend it dealing with biggest remaining risk to the programme, whatever that might be. Never put off until tomorrow the experiment that could kill the programme. Do it now.
Too often, inventors are seduced by the elegance of their ideas, and the excitement generated by the initial efficacy data. Believing it may be their passport to financial support for their research, to delivering their desire to make a difference and perhaps even underpinning personal financial independence, there is a natural reticence to blow a whole in the side of the ship. The longer she can be kept afloat, they reason, the better – and perhaps we will anyway by then have accumulating enough information to circumvent whatever flaws might be uncovered in the programme.
Such a strategy does not work. It doesn’t work for the investor (whether government, charity or commercial) because money is being spent on a programme that might fail later for reasons that could have been identified sooner. Equally, it doesn’t work for the inventor, who is wasting their innovative capacity on a project that (though they don’t yet know it) is doomed to fail.
Developing drugs is a long-winded affair – at least a decade from idea to marketplace, and quite often two decades. You cannot fit many of those into an entire career. The opportunity cost for the individual innovator is therefore massive if they cling tightly to one idea long after it should have been killed.
So the interests of the investor and the innovator are aligned: the data package has to remain “in balance”. There are several threads to each product that must all come together at the end to achieve registration of a new drug: principally, you have to demonstrate sufficient efficacy in a commercially-viable disease population with the right molecule (in terms of pharmaceutical properties such as cost of goods and dose and regimen), with an acceptable therapeutic index and side-effect profile. There is absolutely no point trying to complete one such thread while lagging behind in the others. They need to be progressed together, always asking which thread currently represents the greatest risk to the success of the project, and advancing that thread as the priority.
Back to the early stage invention, then, the product opportunity is only defined by the target and the early evidence of efficacy. But as soon as a promising candidate has been identified, the question of “will it work” (though far from proven) is no longer the biggest risk. That honour switches to “will it be safe”.
So by the time you compile a project proposal to send to funding bodies, the focus will be heavily on the safety of the mechanism (as opposed to the safety of the molecule). It is harder therefore to make a positive assessment of the prospects for such a project if there is virtually no information relating to safety.
Of course, safety (like efficacy) is a multi-faceted question. The two most important components of safety are target-dependent and target-independent. For most early stage projects, the target-independent (that is, molecule or chemotype-specific) toxicology is much less important. There is no certainty that the initially proposed agent will be the one actually developed. But the toxicology of the target is critical.
Too often the limit of the available target-specific safety data is that the knockout animal survives into adulthood, or that animals treated with the proposed agent survived the treatment period. But that’s not really enough: it is hard to think of any target where there is not a specific theoretical concern. Agents that target complement pathways to halt transplant rejection would likely risk triggering autoimmune reactions. Anti-inflammatory agents risk increasing susceptibility to infection. Agents targeting mTOR to inhibit proliferation in cancer risk causing immunosuppression. If you don’t address such theoretical concerns, preferably with data, then they will sink your project.
Why is there such reluctance to provide such data?
The problem is principally one of perception. To an early stage innovator, safety carries connotations of hERG assays, Ames Tests and GLP toxicology studies. Safety pharmacology is principally a test of molecule-specific toxicity. Conventional toxicology studies will pick up some target-specific side-effects, but they are certainly not comprehensive. They are also lengthy and expensive. In the end, for many projects they do not properly de-risk the specific concerns in any case.
The solution is simple. Address the critical target-specific safety issues in the same animals used to make the first demonstration of efficacy. You absolutely cannot do conventional toxicology (elevating doses until toxicity is observed) in this way, and adding safety end-points to an efficacy study in no way reduces the demands of the GLP toxicology studies that will be required for IND.
But you can polarize the outcome of the assessment of your early stage project by people like me. If the concerns about possible side-effects of the mechanism are proved to be real the project may be dead – and that’s good for the innovator as well as the investor. Yet if the data suggests there is a decent therapeutic index between the interesting signs of efficacy and these mechanism-based side-effects your project will have been catapulted into the top division of candidates for further development.
Whether this increased focus on safety means a more detailed theoretical treatise to replace the couple of sentences in the typical early-stage business plan, or a few carefully chosen additional measures in your animal studies, or indeed a more sophisticated combination study design to probe efficacy and safety simultaneously to control costs, the return on that effort will be worthwhile.
So please do not assume that de-risking the safety component of a project means waiting until formal toxicity or safety pharmacology studies. Give me more information, and preferably some new data, to support the proposition that your first-in-class innovative product candidate can deliver a viable therapeutic index and your likelihood of getting a positive review from people like me will increase significantly.
I cannot promise to like every new target, but if there is insufficient attention to the safety consequences of intervening on that target you can be fairly confident that the review will be negative.