Antibiotic Trial Designs - Rex, Shlaes Part 2

See my previous blog.  Today, I want to look at other ways to skin this cat. These ideas are mostly mine – but again, John Rex was my sounding board.

As  background, I highly recommend viewing the video of the presentation by Ellenberg presented at an NIH conference on trial designs for emerging infectious diseases.  It is very informative. The statistical problems for such trials are numerous but hinge on the following assumption that we must try and meet/validate – that the distribution of patients with good vs. poor prognoses are the same in the experimental and control groups. This is a key basis for preferring a randomized trial. In designing trials to address rare infections, rare pathogens, and pathogen-specific indications, the patient numbers may not be able to support a randomized design. We might not even be able to achieve statistical inference with an externally controlled design – but, in my view, this is where we will have to go. According to the paper by Byar (requires subscription) and later Elllenberg, an externally controlled trial design can be justified if the following conditions can be met . .

·      A randomized trial is infeasible because of the rarity of the condition under study.

·      There must be sufficient experience to ensure that patients not receiving therapy will have a uniformly poor prognosis.

·      The therapy must not be expected to have substantial side effects.

·      There must be a justifiable expectation that the potential benefit to the patient will be sufficiently large to make interpretation of the results of a non-randomized trial unambiguous.

·      The scientific rationale for the treatment must be sufficiently strong that a positive result would be widely expected.

I would argue that a new antibiotic expected to be active against resistant pathogens would meet these criteria assuming it had been shown to be safe in a sufficient number of volunteers/patients.  The data supporting a lack of efficacy of antibiotics where the exposure (drug levels) obtained are not high enough for the MIC (“susceptibility”) of the pathogen are clear and overwhelming.

Most of the failures of externally controlled trials to provide reliable results have resulted from inadequate controls.

·      Controls had been derived from a different time such that control therapy had changed by the time the actual trial was conducted;

·      Or supportive care had changed altering prognosis for controls.

·      Effect size in controls had simply been underestimated for other reasons.

How can we overcome these obstacles for antibacterial drugs?

• ·Get your PK/PD house in order. If you buy the UDR vs. XDR argument from the previous blog, then we can use PK/PD to show that pathogens resistant to comparator agents will be effectively treated by our experimental drug. .
• o   Have clearly and adequately designed PK/PD targets.

o Make sure you have adequate PK in the population you intend to treat (possibly studying the PK of the new antibiotic PK as an add-on to the SOC or comparator to be used as a control  in your proposed study).

·      Consider a small, open label phase II study to help convince physicians and regulators that your new antibiotic will, in fact, benefit patients as you expect based on PK/PD considerations. This will also bolster your PK/PD argument and may even provide an early look at efficacy.

·      Define your inclusion/exclusion criteria early.  I would advise being expansive rather than constrictive here – you don’t want a lot of amendments in the middle of your pivotal trial – this is not non-inferiority.

·      Carry out a retrospective (within the previous year or two) observational study of the key patient population treated with SOC or with comparator drug to define control level of response.  This should be done in centers likely to participate in the trial to remove center-to-center bias as much as possible.

·      Early in the trial, carry out a prospective study of SOC or comparator to validate the assumptions you have made about controls during your retrospective SOC – obviously this is done in centers actually participating (and contributing patients to) in the ongoing trial.

The alternatives discussed by Ellenberg such as cluster-controlled trials and adaptive allocation randomization designs all require more patients than we will ever have available to study.

If, in fact, we observe a large treatment effect early, I would wonder - is it still ethical to continue the trial? -  even if statistical inference has not yet been achieved?

Based on my previous discussions with FDA, and John Rex’s feedback, it is possible if not likely that the FDA will balk at externally controlled trials even though these would be allowed in the context of their unmet needs guidance. (Then, of course, that section should be removed). The FDA needs to see -“Substantial evidence of efficacy through adequate and well-controlled investigations . . .” and they may consider that the approach I have outlined above will not meet that criteria.  (Since those adjectives [subtantial, adequate, well-controlled] are not so well defined – I’m not sure how they get to that particular place.)

Alternatives that might be more palatable to FDA might include a non-inferiority trial with wide margins.  For example, a trial powered at 80% with a margin of 25%, even with only 60% evaluable, will only require 67 patients per arm or 134 patients total.  Obviously, one would still need a 300 patient safety database . . .

Another possibility might be an altered randomization ratio like 2:1, 3:1 or even 4:1.  But here – one might consider approval based on a P value of 0.1 – what is so magical about P=.05?

Based on these thoughts, for the right drug, where the population to be studied will be highly restricted, I recommend negotiating a design with Europe, carrying out your trials and then presenting it to FDA as a fait accompli.

Finally, I plea once again for congress to stay out of the way!