Yesterday, Roche (OTCQX:RHHBY) announced its decision to discontinue its Phase 3 study of gantenerumab, its experimental anti-amyloid antibody, in early Alzheimer’s Disease. The study failed a futility analysis – the clearest possible evidence of a lack of signal.
This marks the latest nadir for the amyloid hypothesis – the dominant collective understanding of the molecular pathogenesis of Alzheimer’s Disease for more than two decades. A hypothesis that has remained the mainstream opinion in the face of the most extraordinary amount of negative data. Proof, if proof were needed, that some hypotheses have a status beyond disproval.
There are lots of good, if circumstantial, reasons to believe in the importance of beta-amyloid in dementia – not least because the brains of sufferers are stuffed full of it. It was, therefore, a very reasonable proposition that antibodies capable of clearing beta-amyloid from the brain would be a breakthrough therapy for what is certain to be the global epidemic of the 21st Century.
The pharmaceutical industry responded by generating the necessary antibodies, and demonstrated some impressive effects: Both Lilly’s (NYSE:LLY) solanezumab and bapineuzumab from Pfizer (NYSE:PFE) and J&J (NYSE:JNJ) substantially reduced beta-amyloid in phase 2 trials. That anti-amyloid antibodies clear beta-amyloid is not in doubt (although that simple statement itself belies a layer of complexity: beta-amyloid is not one substance but a family of related substances, some of which are cleared with certain antibodies and others, most likely, are not).
Thus emboldened, a number of these anti-amyloid antibodies were advanced into large, lengthy and eye-wateringly expensive Phase 3 clinical trials. The goal was to demonstrate an improvement in cognition (functions such as memory, which are progressively lost in dementia). The omens were surely excellent: after all, it was clear the agents did what it said on the tin (cleared amyloid) and the hypothesis itself was gold-plated.
But then the trials started to read out, and the picture was uniformly negative. By 2012 we had several huge Phase 3 trials with a couple of different anti-amyloid antibodies from different companies – and a slew of negative data.
What happened next was very interesting.
Instead of drawing the obvious conclusion (that the amyloid hypothesis was false), the assembled masses began casting around for a different explanation for the surprising failure. Some pointed at the affinity of the antibodies that had failed in Phase 3 and argued that a “better” antibody would have yielded a different outcome (even though even the lowest affinity antibody had been shown to clear amyloid in Phase 2 studies). Others suggested that the antibodies had cleared the wrong KIND of beta-amyloid, leaving the dangerous sub-fraction in place.
But perhaps the most common flotsam that the deniers clung on to was the post hoc analysis of the Phase 3 trial data. Trials (in Alzheimer’s Disease or any other indication) have a primary end-point: a pre-defined objective to see an effect on one measured parameter in the whole population studied. In the case of the anti-amyloid trials this was some measure of cognition in the patients with established Alzheimer’s Disease treated with the drug candidates.
Trials have a pre-specified objective for a reason. The statistical analysis depends on only testing one hypothesis. If you cast around afterwards asking other questions of the data, then eventually – for certain – you will find a pattern by chance alone. This is post hoc data analysis.
Desperate (it seems) to salvage some hope from a very bleak situation, a post hoc analysis of the data from the EXPEDITION trials with solanezumab was undertaken. And unsurprisingly, it found something “interesting”: there was evidence of an effect on cognition in the patients with the mildest disease (even though there was no effect on cognition when considering the entire trial population).
This olive branch was seized with both hands. The amyloid believers were quick to suggest that the problem was not with their beloved hypothesis, but only that they had treated the patients too late in the progression of the disease. Once a certain amount of cognitive capacity had been lost, and a certain amount of damage done to the brain architecture, they reasoned, then clearly removing the amyloid deposits after that point would be fruitless. And so it had turned out (at least when looked at through the rose-tinted spectacles of post hoc analysis).
It didn’t matter (to them) that another trial that had already recruited only these milder Alzheimer’s Disease cases also failed. That was easy to overlook. In the rush to adopt any world-view other than one that questioned the foundation of the amyloid hypothesis itself, the mainstream view settled on the proposition that if only anti-amyloids were tested on people before Alzheimer’s Disease were established (and before irreversible damage had occurred) then the outcome would be very different.
And so a new generation of large, lengthy and eye-wateringly expensive Phase 3 trials with anti-amyloid agents were conceived and implemented – the first of which to provide any data was the SCarlet roAD trial using gantenerumab from Roche’s Genentech unit. This was a study in so-called “pro-dromal” Alzheimer’s Disease: a population suffering mild cognitive impairment (MCI), which left untreated would in many instances progress to full-blown Alzheimer’s Disease. SCarlet roAD was, therefore, the first test of the “amyloid hypothesis 2.0”.
And the abject failure of this latest study to improve cognition in this population would seem to hole even the modified amyloid hypothesis below the waterline. Further trials are due to report over the coming years, and while its possible they will deliver materially better results, it would be a brave man who bet on that outcome now. Few argue that the Genentech antibody is an inferior beast, although of course one could still argue that it misses the “key” sub-fraction of beta-amyloid.
It will be interesting to see how the scientific community responds. For some, no doubt, even this data will not be enough to abandon a decades-old, much cherished hypothesis. Biology is complex enough that there is always wiggle room – you can never prove that a hypothesis is wrong, only that it is increasingly unlikely to be true. But for the rational majority, it is time to recognize that this particular emperor really is naked. Failure to do so risks sinking even more capital into this dead-end.
There are a few important lessons from this sorry tale, that extend well beyond Alzheimer’s Disease. It highlights the danger of what I previously called “idea bubbles” – that a hypothesis gains so much credibility over a long period of time that even when the data tells you otherwise, adherents (acolytes may be a better word) question everything but the hypothesis.
Secondly, it highlights the danger of post hoc analysis of clinical trial data. This particular poison pervades late stage drug development, and is driven by the deep human bias against accepting losses. The result, as with the anti-amyloids, is billions of dollars “invested” in ultimately unproductive programs long after any realistic hope of success has gone. Arguably this is the biggest single cause of low capital productivity in pharmaceutical R&D. Investors, in particular, need to learn to recognize this form of cultured hara-kiri and run a mile.
Lastly, and perhaps most importantly, it should teach us that wanting something badly is not enough reason to discard our usual standards of rational thinking. Pharmaceutical company bosses and politicians alike rightly emphasize the societal cost of Alzheimer’s Disease – which can only grow substantially in the future. Finding a cure for Alzheimer’s Disease is, arguably, the most important goal for mankind in the 21st Century. But wanting a solution to the problem is not enough. We still have to tackle the problem in the right way.
Lowering the bar of proof for initiating large and expensive clinical studies is counter-productive. Valuable resources are then very likely to wasted (as has been the case with anti-amyloids). Finding a cure for Alzheimer’s Disease is not a problem you can “go through” but rather one you have to “go round”. What the world needs right now is a meaningful surrogate for efficacy in Alzheimer’s Disease, whether a predictive clinical marker that can be examined in small, short and cheap Phase 2 trials, or a gateway indication, where success in a rare neurological condition predicts efficacy in the vast Alzheimer’s Disease indication.
Let us hope that the latest trial failure finally delivers the change in mindset we so badly need.
This article by DrugBaron was original published by Forbes, and can be found here
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