'Failing Fast' and Moving Forward: Setting the Right Pace for Clinical Cancer Research

H. Jack West, MD


March 14, 2016

"The fastest way to succeed is to double your rate of failure."
—Thomas Watson, Sr, taken from
Whoever Makes the Most Mistakes Wins: The Paradox of Innovation

I recently returned from the International Association for the Study of Lung Cancer (IASLC) Targeted Therapies in Lung Cancer Conference, a meeting with an unusual format: a 3-day marathon of mostly 5-minute presentations on as many new agents and treatment strategies for lung cancer as possible, tied together with discussions of the underlying science and future directions of various drug classes. Over the past several years, we have seen an ever-growing number of targets and agents move from aspirational strategies to effective treatment agents; in fact, we have achieved so many successes with new targets like ALK and ROS1 rearrangements, with novel treatments for acquired resistance in T790M-positive EGFR mutations, and of course now with immunotherapies for lung cancer, that our expectations have risen markedly.

In one session of this conference, however, I and other faculty presented summaries of heat shock protein (HSP) 90 inhibitors, alone or in combination with other agents, that ultimately became a litany of disappointing data and failed studies, most in relatively early phases of development. We joked uncomfortably about our shared disappointment, but I would argue that we should be happy that the system worked, even if these agents don't move forward. We were able to ask questions about the efficacy and feasibility of treating a wide range of patients with various HSP90 inhibitors and obtained a clear answer in a timely way. And we can now move on.

True innovators embrace failure as a learning experience.

A press release[1] was just issued noting that Peregrine Pharmaceuticals has recently discontinued the SUNRISE trial of docetaxel alone or in combination with the investigational immunotherapeutic agent bavituximab—a chimeric monoclonal antibody against phosphatidylserine. This decision was based on the recommendation of the independent data monitoring committee (IDMC) for the trial, as a result of an analysis demonstrating that preliminary data were not consistent with a survival benefit despite tremendous media hype of phase 2 data with this agent.[2] While this is a regrettable result, the IDMC did exactly what it was charged with doing, and we received a timely answer, even if it wasn't the one we or our lung cancer patients would have wanted.

True innovators embrace failure as a learning experience. The goal shouldn't be to focus on where you know you can win to avoid failure, but rather to "fail fast."

Test ideas, get quick feedback on whether an approach is worth pursuing, and then cut your losses and move on if the answer is no.

We rightfully bemoan the development of far too many "me too" drugs as well as trials that produce statistically but not clinically significant benefits for our patients or focus on dubious, manufactured trial endpoints that simply move the goal posts forward and compromise what should be high standards for introducing a new therapy, especially as the cost of our cancer treatments steadily escalates over time. But we must also recognize that while it is enviable that we have come so far from the days a decade or more ago when the failure of clinical trial after trial in advanced lung cancer seemed almost preordained, the pendulum may now have swung too far in the other direction: We cannot rightfully expect to hit the mark every time. If we do, we aren't aiming high enough.

Novel clinical research needs to be conducted at the optimal pace. At this same IASLC Targeted Therapies meeting, the audience heard summaries of the trial portfolio of multiple companies, each with their own immune checkpoint inhibitor against the programmed cell death protein-1 (PD-1)/programmed death ligand-1 (PD-L1) axis with the same or similar mechanism of action as many others. Trial after trial, each with a remarkably similar design testing a different agent with or against chemotherapy or a standard targeted therapy, is now being conducted. Every company with an immunotherapy agent seems to be stampeding into phase 3 trials based on little more than an absence of prohibitive toxicity in phase 1 combination trials of a few patients and the sheer existence of both the new agent and a current standard of care. Presenters joked that it was sometimes difficult to justify any premise of a compelling rationale for such trials, and especially for the fourth iteration of a trial combining platinum doublet chemotherapy with a PD-1 or PD-L1 inhibitor.

Every company with an immunotherapy agent seems to be stampeding into phase 3 trials based on little more than an absence of prohibitive toxicity in phase 1 combination trials of a few patients and the sheer existence of both the new agent and a current standard of care.

With so many PD-1 or PD-L1-directed immune checkpoint inhibitors failing thus far to distinguish their clinical activity or spectrum of adverse effects, it is difficult to envision a situation in which the lung cancer community is well served by an approach to clinical development so dissociated from critical feedback questioning whether it is wise to develop randomized phase 3 trials at such a frenzied pace. The development strategies for not one but multiple immunotherapy agents arise from a pharmaceutical gold rush mentality that exists despite our inability to reliably identify which patients are most likely to benefit or exclude those who will not, and despite the absence of any truly compelling evidence of a synergistic benefit from immunotherapy with concurrent chemotherapy or other prevailing standards of care.

I have reflected previously on figitumumab[3] and other agents that proved to be dismal failures in large randomized trials, in large part because their development was rushed ahead of the clinical evidence to support them. Even when thinking about an agent such as bevacizumab, with proven utility against multiple cancers, it is sobering to consider how development of this agent may have been aborted if careful assessment of phase 2 data had not revealed an association with squamous histology[4] that led to significant modifications of future trials, thereby keeping bevacizumab from being remembered primarily as an agent associated with prohibitive risk for fatal hemoptysis. There is potential harm in rushing the drug development process, without availing ourselves of the benefit of feedback from smaller trials and heeding their results.

Even if these trials show significant benefits, the redundancy in clinical trials, such as in the immunotherapy space currently, occurs primarily to ensure that every company with its own version of the same therapy can squeeze its way to a seat at the table of a specific clinical setting. Though we might hope that such "me too" designs could provide a benefit in terms of pricing agents that should be in competition, the escalating trajectory of very aggressively priced cancer therapies should lead us to be skeptical of such an argument, even though it might provide at least a weak justification for pursuing multiple trials of the same design in parallel for so many versions of what seem to be interchangeable therapies.

The goal of clinical research in cancer cannot be to conduct trials the fastest, or to achieve the largest number of positive trials by running multiple versions of the same trial, or lowering our standards by dissociating statistical from clinical significance, or accepting endpoints that divert our attention from the endpoints that truly matter. Our goal should be to pursue the most efficient use of time, money, and patient resources to test truly novel approaches systematically, including welcoming the feedback of results from early studies with a critical eye. This should include accepting failure as the way to move forward.


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