While we're talking about AstraZeneca, here's a look at their recent drug development history from the inside. The company had undertaken a complete review of its portfolio and success rates (as well they might, given how things have been going overall).
In this article, we discuss the results of a comprehensive longitudinal review of AstraZeneca's small-molecule drug projects from 2005 to 2010. The analysis allowed us to establish a framework based on the five most important technical determinants of project success and pipeline quality, which we describe as the five 'R's: the right target, the right patient, the right tissue, the right safety and the right commercial potential. A sixth factor — the right culture — is also crucial in encouraging effective decision-making based on these technical determinants. AstraZeneca is currently applying this framework to guide its R&D teams, and although it is too early to demonstrate whether this has improved the company's R&D productivity, we present our data and analysis here in the hope that it may assist the industry overall in addressing this key challenge.
That already gets things off to a bad start, in my opinion, because I really hate those alliterative "Five Whatevers" and "Three Thingies" that companies like to proclaim. And that's not just because Chairman Mao liked that stuff, although that is reason enough to wonder a bit. I think that I suffer from Catchy Slogan Intolerance, a general disinclination to believe that reality can be usefully broken down into discrete actions and principles that just all happen to start with the same letter. I think these catchphrases quantify the unquantifiable and simplify what shouldn't be simplified. The shorter, snappier, and more poster-friendly the list of recommendations, the less chance I think they have of being any actual use. Other than setting people's teeth on edge, which probably isn't the goal.
That said, this article itself does a perfectly good job of laying out many of the things that have been going wrong in the big pharma organizations. See if any of this rings a bell for you:
. . .However, with the development of high-throughput and ultra-high-throughput screening and combinatorial chemistry approaches during the 1980s and 1990s, as well as the perception that a wealth of new targets would emerge from genomics, part of this productivity issue can also be attributed to a shift of R&D organizations towards the 'industrialization' of R&D. The aim was to drive efficiency while retaining quality, but in some organizations this led to the use of quantity-based metrics to drive productivity. The hypothesis was simple: if one drug was launched for every ten candidates entering clinical development, then doubling or tripling the number of candidates entering development should double or triple the number of drugs approved. However, this did not happen; consequently, R&D costs increased while output — as measured by launched drugs — remained static.
This volume-based approach damaged not only the quality and sustainability of R&D pipelines but, more importantly, also the health of the R&D organizations and their underlying scientific curiosity. This is because the focus of scientists and clinicians moved away from the more demanding goal of thoroughly understanding disease pathophysiology and the therapeutic opportunities, and instead moved towards meeting volume-based goals and identifying an unprecedented level of back-up and 'me too' drug candidates. In such an environment, 'truth-seeking' behaviours to understand disease biology may have been over-ridden by 'progression-driven' behaviours that rewarded scientists for meeting numerical volume-based goals.
Thought so. Pause to shiver a bit (that's what I did - it seemed to help). The AZ team looked at everything that had been active during the 2005-2010 period, from early preclinical up to the end of Phase II. What they found, compared to the best figures on industry averages, was that the company looked pretty normal in the preclinical area (as measured by number of projects and their rates of progression, anyway), and that they actually had a higher-than-usual pass rate through Phase I. Phase II, though, was nasty - they had a noticeably higher failure rate, suggesting that too many projects were being allowed to get that far. And although they weren't explicitly looking looking beyond Phase II, the authors do note that AZ's success rate at getting drugs all the way to market was significantly lower than rest of the industry's as well.
The biggest problem seemed to be safety and tox. This led to many outright failures, and to other cases where the human doses ended up limited to non-efficacious levels.
During preclinical testing, 75% of safety closures were compound-related (that is, they were due to 'off-target' or other properties of the compound other than its action at the primary pharmacological target) as opposed to being due to the primary pharmacology of the target. By contrast, the proportion of target-related safety closures rose substantially in the clinical phase and was responsible for almost half of the safety-related project closures. Such failures were often due to a collapse in the predicted margins between efficacious doses and safety outcomes, meaning it was not possible to achieve target engagement or patient benefit without incurring an unacceptable safety risk.
On top of this problem, an unacceptable number of compounds that made it through safety were failing in Phase II though lack of efficacy. There's a good analysis of how this seems to have happened, but a big underlying factor seems to have been the desire to keep progressing compounds to meet various targets. People kept pushing things ahead, because things had to be pushed ahead, and the projects kept being scooting along the ground until they rolled off into one ravine or another.
And I think that everyone with some experience in this business will know exactly what that feels like - this is not some mysterious ailment that infected AstraZeneca, although they seem to have had a more thorough case of it than usual. Taking the time to work out what a safety flag might be telling you, understand tricky details of target engagement, or figure out the right patient population or the right clinical endpoint - these things are not always popular. And to be fair, there are a near-infinite number of reasons to slow a project down (or stop it altogether), and you can't stop all of them. But AZ's experience shows, most painfully, that you can indeed stop too few of them. Here's a particularly alarming example of that:
In our analysis, another example of the impact of volume-based goals could be seen in the strategy used to select back-up drug candidates. Back-up molecules are often developed for important projects where biological confidence is high. They should be structurally diverse to mitigate the risk for the programme against compound-related issues in preclinical or early development, and/or they should confer some substantial advantage over the lead molecule. When used well, this strategy can save time and maintain the momentum of a project. However, with scientists being rewarded for the numbers of candidates coming out of the research organization, we observed multiple projects for which back-up molecules were not structurally diverse or a substantial improvement over the lead molecule. Although all back-up candidates met the chemical criteria for progression into clinical testing, and research teams were considered to have met their volume-based goals, these molecules did not contribute to the de-risking of a programme or increase project success rates. As a consequence, all back-up candidates from a 'compound family' could end up failing for the same reason as the lead compound and indeed had no higher probability of a successful outcome than the original lead molecule (Fig. 6). In one extreme case, we identified a project with seven back-up molecules in the family, all of which were regarded as a successful candidate delivery yet they all failed owing to the same preclinical toxicology finding. This overuse of back-up compounds resulted in a highly disproportionate number of back-up candidates in the portfolio. At the time of writing, approximately 50% of the AstraZeneca portfolio was composed of back-up molecules.
I'm glad this paper exists, since it can serve as a glowing, pulsing bad example to other organizations (which I'm sure was the intention of its author, actually). This is clearly not the way to do things, but it's also easy for a big R&D effort to slip into this sort of behavior, while all the time thinking that it's doing the right things for the right reasons. Stay alert! The lessons are the ones you'd expect:
An underlying theme that ran through the interviews with our project teams was how the need to maintain portfolio volume led to individual and team rewards being tied to project progression rather than 'truth-seeking' behaviour. The scientists and clinicians within the project teams need to believe that their personal success and careers are not intrinsically linked to project progression but to scientific quality, smart risk-taking and good decision-making.
But this is not the low energy state of a big organization. This sort of behavior has to be specifically encouraged and rewarded, or it will disappear, to be replaced by. . .well, you all know what it's replaced by. The sort of stuff detailed in the paper, and possibly even worse. What's frustrating is that none of these are new problems that AZ had to discover. I can bring up my own evidence from twelve years ago, and believe me, I was late to the party complaining about this sort of thing. Don't ever think that it can't happen some more.