Clinical trials

Randomized trials of parachute use

Posted on by John

It is widely assumed that parachute use improves your chances of surviving a leap from an airplane. However, a meta analysis suggests this practice is not adequately supported by controlled experiments. See the article Parachute use to prevent death and major trauma related to gravitational challenge: systematic review of randomized controlled trials by Gordon C S Smith and Jill P Pell. The authors summarize their conclusions in the abstract.

As with many interventions intended to prevent ill health, the effectiveness of parachutes has not been subjected to rigorous evaluation by using randomised controlled trials. Advocates of evidence based medicine have criticised the adoption of interventions evaluated by using only observational data. We think that everyone might benefit if the most radical protagonists of evidence based medicine organised and participated in a double blind, randomised, placebo controlled, crossover trial of the parachute.

Dose-finding: why start at the lowest dose?

Posted on by John

You’ve got a new drug and it’s time to test it on patients. How much of the drug do you give? That’s the question dose-finding trials attempt to answer.

The typical dose-finding procedure starts by selecting a small number of dose levels, say four or five. The trial begins by giving the lowest dose to the first few patients, and there is some procedure for deciding when to try higher doses. Convention says it is unethical to start at any dose other than lowest dose. I will give several reasons to question convention.

Suppose you want to run a clinical trial to test the following four doses of Agent X: 10 mg, 20 mg, 30 mg, 50 mg. You want to start with 20 mg. Your trial goes for statistical review and the reviewer says your trial is unethical because you are not starting at the lowest dose. You revise your protocol saying you only want to test three doses: 20 mg, 30 mg, and 50 mg. Now suddenly it is perfectly ethical to start with a dose of 20 mg because it is the lowest dose.

The more difficult but more important question is whether a dose of 20 mg of Agent X is medically reasonable. The first patient in the trial does not care whether higher or lower doses will be tested later. He only cares about the one dose he’s about to receive. So rather than asking “Why are you starting at dose 2?” reviewers should ask “How did you come up with this list of doses to test?”

A variation of the start-at-the-lowest-dose rule is the rule to always start at “dose 1”. Suppose you revise the original protocol to say dose 1 is 20 mg, dose 2 is 30 mg, and dose 3 is 50 mg. The protocol also includes a “dose −1” of 10 mg. You explain that you do not intend to give dose −1, but have included it as a fallback in case the lowest dose (i.e. 20 mg) turns out to be too toxic. Now because you call 20 mg “dose 1” it is ethical to begin with that dose. You could even begin with 30 mg if you were to label the two smaller doses “dose −2” and “dose −1.” With this reasoning, it is ethical to start at any dose, as long as you call it “dose 1.” This approach is justified only if the label “dose 1” carries the implicit endorsement of an expert that it is a medically reasonable starting dose.

Part of the justification for starting at the lowest dose is that the earliest dose-finding methods would only search in one direction. This explains why some people still speak of “dose escalation” rather than “dose-finding.” More modern dose-finding methods can explore up and down a dose range.

The primary reason for starting at the lowest dose is fear of toxicity. But when treating life-threatening diseases, one could as easily justify starting at the highest dose for fear of under treatment. (Some trials do just that.) Depending on the context, it could be reasonable to start at the lowest, highest, or any dose in between.

The idea of first selecting a range of doses and then deciding where to start exploring seems backward. It makes more sense to first pick the starting dose, then decide what other doses to consider.

Related: Adaptive clinical trial design

Innovation II

Posted on by John

In 1601, an English sea captain did a controlled experiment to test whether lemon juice could prevent scurvy.  He had four ships, three control and one experimental.  The experimental group got three teaspoons of lemon juice a day while the control group received none. No one in the experimental group developed scurvy while 110 out of 278 in the control group died of scurvy. Nevertheless, citrus juice was not fully adopted to prevent scurvy until 1865.

Overwhelming evidence of superiority is not sufficient to drive innovation.

Source: Diffusion of Innovations

False positives for medical papers

Posted on by John

My previous two posts have been about false research conclusions and false positives in medical tests. The two are closely related.

With medical testing, the prevalence of the disease in the population at large matters greatly when deciding how much credibility to give a positive test result. Clinical studies are similar. The proportion of potential genuine improvements in the class of treatments being tested is an important factor in deciding how credible a conclusion is.

In medical tests and clinical studies,  we’re often given the opposite of what we want to know. We’re given the probability of the evidence given the conclusion, but we want to know the probability of the conclusion given the evidence. These two probabilities may be similar, or they may be very different.

The analogy between false positives in medical testing and false positives in clinical studies is helpful, because the former is easier to understand that the latter. But the problem of false conclusions in clinical studies is more complicated. For one thing, there is no publication bias in medical tests: patients get the results, whether positive or negative. In research, negative results are usually not published.

Population drift

Posted on by John

The goal of a clinical trial is to determine what treatment will be most effective in a given population. What if the population changes while you’re conducting your trial? Say you’re treating patients with Drug X and Drug Y, and initially more patients were responding to X, but later more responded to Y. Maybe you’re just seeing random fluctuation, but maybe things really are changing and the rug is being pulled out from under your feet.

Advances in disease detection could cause a trial to enroll more patients with early stage disease as the trial proceeds. Changes in the standard of care could also make a difference. Patients often enroll in a clinical trial because standard treatments have been ineffective. If the standard of care changes during a trial, the early patients might be resistant to one therapy while later patients are resistant to another therapy. Often population drift is slow compared to the duration of a trial and doesn’t affect your conclusions, but that is not always the case.

My interest in population drift comes from adaptive randomization. In an adaptive randomized trial, the probability of assigning patients to a treatment goes up as evidence accumulates in favor of that treatment. The goal of such a trial design is to assign more patients to the more effective treatments. But what if patient response changes over time? Could your efforts to assign the better treatments more often backfire? A trial could assign more patients to what was the better treatment rather than what is now the better treatment.

On average, adaptively randomized trials do treat more patients effectively than do equally randomized trials. The report Power and bias in adaptive randomized clinical trials shows this is the case in a wide variety of circumstances, but it assumes constant response rates, i.e. it does not address population drift.

I did some simulations to see whether adaptive randomization could do more harm than good. I looked at more extreme population drift than one is likely to see in practice in order to exaggerate any negative effect. I looked at gradual changes and sudden changes. In all my simulations, the adaptive randomization design treated more patients effectively on average than the comparable equal randomization design. I wrote up my results in The Effect of Population Drift on Adaptively Randomized Trials.

Related: Adaptive clinical trial design

Irrelevant uncertainty

Posted on by John

Suppose I asked where you want to eat lunch. Then I told you I was about to flip a coin and asked again where you want to eat lunch. Would your answer change? Probably not, but sometimes the introduction of irrelevant uncertainty does change our behavior.

Here’s an example I’ve seen repeatedly. In adaptive clinical trials, a patient’s treatment is influenced by the data on all previous patients. It is often the case that a particular observation has no immediate impact. Suppose Mr. Smith’s outcome is unknown. We calculate what the treatment for the next patient will be if Mr. Smith responds well and what it will be if he does not. If both doses are the same, why wait to know his outcome before continuing? Some people accept this reasoning immediately, but others are quite resistant.

Not only may a patient’s outcome be irrelevant, the outcome of an entire clinical trial may be irrelevant. I heard of a conversation with a drug company where a consultant asked what the company would do if their trial were successful. He then asked what they would do if it were not successful. Both answers were the same. He then asked why do the trial at all, but his question fell on deaf ears.

While it is irrational to wait to resolve irrelevant uncertainty, it is a human tendency. For example, businesses may delay a decision on some action pending the outcome of a presidential election, even if they would take the same action regardless which candidate won. I see how silly this is when other people do it, but it’s not too hard for me to think of analogous situations where I act the same way.