Multi-arm adaptively randomized clinical trials

This post will look at adaptively randomized trial designs. In particular, we want to focus on multi-arm trials, i.e. trials of more than two treatments. The aim is to drop the less effective treatments quickly so the trial can focus on determining which of the better treatments is best.

We’ll briefly review our approach to adaptive randomization but not go into much detail. For a more thorough introduction, see, for example, this report.

Why adaptive randomization

Adaptive randomization designs allow the randomization probabilities to change in response to accumulated outcome data so that more subjects are assigned to (what appear to be) more effective treatments. They also allow for continuous monitoring, so one can stop a trial early if we’re sufficiently confident that we’ve found the best treatment.

Adapting randomization probabilities

Of course we don’t know what treatments are more effective or else we wouldn’t be running a clinical trial. We have an idea based on the data seen so far at any point in the trial, and that assessment may change as more data become available.

We could simply put each patient on what appears to be the best arm (the “play-the-winner” strategy), but this would forgo the benefits of randomization. Instead we compromise, continuing to randomize, but increasing the randomization probability for what appears to be the best treatment at the time a subject enters the trial.

Continuous monitoring

By monitoring the performance of each treatment arm, we can drop a poorly performing arm and assign subjects to the better treatment arms. This is particularly important for multi-arm trials. We want to weed out the poor treatments quickly so we can focus on the more promising treatments.

Continuous monitoring opens the possibility of stopping trials early if there is a clear winner. If all treatments perform similarly, more patients will be used. The maximum number of patients will be enrolled only if necessary.

Multi-arm trials

Randomizing an equal number of patients to each of several treatment arms would require a lot of subjects. A multi-arm adaptive trail turns into a two-arm trial once the other arms are dropped. We’ll present simulation results below that demonstrate this.

Running a big trial with several treatment arms could be more cost effective than running several smaller trials because there is a certain fixed cost associated with running any trial, no matter how small: protocol review, IRB approval, etc.

There has been some skepticism whether two-arm adaptively randomized trials live up to their hype. Trial design is a multi-objective optimization problem and it’s easy to claim victory by doing better by one criteria while doing worse by another. In my opinion, adaptive randomization is more promising for multi-arm trials than two-arm trials.

In my experience, multi-arm trials benefit more from early stopping than from adapting randomization probabilities. That is, one may treat more patients effectively by randomizing equally but dropping poorly performing treatments. Instead of reducing the probability of assigning patients to a poor treatment arm, continue to randomize equally so you can more quickly gather enough evidence to drop the arm.

I initially thought that gradually decreasing the randomization probability of a poorly performing arm would be better than keeping the randomization probability equal until it suddenly drops to zero. But experience suggests this intuition was wrong.

Simulation study

I designed a 4-arm trial with a uniform prior on the probability of response on each arm. The maximum accrual was set to 400 patients.

An arm is suspended if the posterior probability of it being best drops below 0.05. (Note: A suspended arm is not necessarily closed. It may become active again in response to more data.)

Subjects are randomized equally to all available arms. If only one arm is available, the trial stops. Each trial was simulated 1,000 times.

In the first scenario, I assume the true probabilities of successful response on the treatment arms are 0.3, 0.4, 0.5, and 0.6 respectively. The treatment arm with 30% response was dropped early in 99.5% of the simulations, and on average only 12.8 patients were assigned to this treatment.

|-----+----------+----------------+----------|
| Arm | Response | Pr(early stop) | Patients |
|-----+----------+----------------+----------|
|   1 |      0.3 |          0.995 | 12.8     |
|   2 |      0.4 |          0.968 | 25.7     |
|   3 |      0.5 |          0.754 | 60.8     |
|   4 |      0.6 |          0.086 | 93.9     |
|-----+----------+----------------+----------|

An average of 193.2 patients were used out of the maximum accrual of 400. Note that 80% of the subjects were allocated to the two best treatments.

Here are the results for the second scenario. Note that in this scenario there are two bad treatments and two good treatments. As we’d hope, the two bad treatments are dropped early and the trial concentrates on deciding the better of the two good treatment.

|-----+----------+----------------+----------|
| Arm | Response | Pr(early stop) | Patients |
|-----+----------+----------------+----------|
|   1 |     0.35 |          0.999 |     11.7 |
|   2 |     0.45 |          0.975 |     22.5 |
|   3 |     0.60 |          0.502 |     85.6 |
|   4 |     0.65 |          0.142 |    111.0 |
|-----+----------+----------------+----------|

An average of 230.8 patients were used out of the maximum accrual of 400. Now 85% of patients were assigned to the two best treatments. More patients were used in this scenario because the two best treatments were harder to tell apart.

Related posts

Valuing results and information

Chris Wiggins gave an excellent talk at Rice this afternoon on data science at the New York Times. In the Q&A afterward, someone asked how you would set up a machine learning algorithm where you’re trying to optimize for outcomes and for information.

Here’s how I’ve approached this dilemma in the past. Information and outcomes are not directly comparable, so any objective function combining the two is going to add incommensurate things. One way around this is to put a value not on information per se but on what you’re going to do with the information.

In the context of a clinical trial, you want to treat patients in the trial effectively, and you want a high probability of picking the best treatment at the end. You can’t add patients and probabilities meaningfully. But why do you want to know which treatment is best? So you can treat future patients effectively. The value of knowing which treatment is best is the increase in the expected number of future successful treatments. This gives you a meaningful objective: maximize the expected number of effective treatments, of patients in the trial and future patients treated as a result of the trial.

The hard part is guessing what will be done with the information learned in the trial. Of course this isn’t exactly known, but it’s the key to estimating the value of the information. If nobody will be treated any differently in the future no matter how the trial turns out—and unfortunately this may be the case—then the trial should be optimized strictly for the benefit of the people in the trial. On the other hand, if a trial will determine the standard of care for thousands of future patients, then there is more value in picking the best treatment.

Bayesian adaptive clinical trials: promise and pitfalls

This afternoon I’m giving a talk at the Houston INFORMS chapter entitled “Bayesian adaptive clinical trials: promise and pitfalls.”

When I started working in adaptive clinical trials, I was very excited about the potential of such methods. The clinical trial methods most commonly used are very crude, and there’s plenty of room for improvement.

Over time I became concerned about overly complex methods, methods which were good for academic publication but may not be best for patients. Such methods are extremely time-consuming to develop and may not perform as well in practice as simpler methods.

There’s a great deal of opportunity between the extremes, methods that are more sophisticated than the status quo without being unnecessarily complex.

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Frequentist properties of Bayesian methods

Bayesian methods for designing clinical trials have become more common, and yet these Bayesian designs are almost always evaluated by frequentist criteria. For example, a trial may be designed to stop early 95% of the time under some bad scenario and stop no more than 20% of the time under some good scenario.

These criteria are arbitrary, since the “good” and “bad” scenarios are arbitrary, and because the stopping probability requirements of 95% and 20% are arbitrary. Still, there’s an idea in lurking in the background that in every design there must be something that is shown to happen no more than 5% of the time.

It takes a great deal of effort to design Bayesian methods with desired frequentist properties. It’s an inverse problem, searching for the parameters in a high-dimensional design space, usually via lengthy simulation, that cause the method to satisfy some criteria. Of course frequentist methods satisfy frequentist criteria by design and so meet these criteria with far less effort. It’s rare to see the tables turned, evaluating frequentist methods by Bayesian criteria.

Sometimes the effort to beat frequentist designs at their own game is futile because the frequentist designs are optimal by their own criteria. More often, however, the Bayesian and frequentist methods being compared are not direct competitors but only analogs. The aim in this case is to match the frequentist method’s operating characteristics by one criterion while doing better by a new criterion.

Sometimes a Bayesian method can be shown to have better frequentist operating characteristics than its frequentist counterpart. This puts dogmatic frequentists in the awkward position of admitting that what they see as an unjustified approach to statistics has nevertheless produced a superior product. Some anti-Bayesians are fine with this, happy to have a procedure with better frequentist properties, even though it happened to be discovered via a process they view as illegitimate.

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Related postBayesian clinical trials in one zip code

Skin in the game for observational studies

The article Deming, data and observational studies by S. Stanley Young and Alan Karr opens with

Any claim coming from an observational study is most likely to be wrong.

They back up this assertion with data about observational studies later contradicted by prospective studies.

Much has been said lately about the assertion that most published results are false, particularly observational studies in medicine, and I won’t rehash that discussion here. Instead I want to cut to the process Young and Karr propose for improving the quality of observational studies. They summarize their proposal as follows.

The main technical idea is to split the data into two data sets, a modelling data set and a holdout data set. The main operational idea is to require the journal to accept or reject the paper based on an analysis of the modelling data set without knowing the results of applying the methods used for the modelling set on the holdout set and to publish an addendum to the paper giving the results of the analysis of the holdout set.

They then describe an eight-step process in detail. One step is that cleaning the data and dividing it into a modelling set and a holdout set would be done by different people than the modelling and analysis. They then explain why this would lead to more truthful publications.

The holdout set is the key. Both the author and the journal know there is a sword of Damocles over their heads. Both stand to be embarrassed if the holdout set does not support the original claims of the author.

* * *

The full title of the article is Deming, data and observational studies: A process out of control and needing fixing. It appeared in the September 2011 issue of Significance.

Update: The article can be found here.

Clinical trial software

This week’s resource post lists some of the projects I managed or contributed to while working at MD Anderson Cancer Center in biostatistics.

If you’d like help with the above software or would like help with clinical trial design, please contact me.

Last week’s resource post: Stand-alone numerical code

Related: Adaptive clinical trial design

 

Finding the best dose

In a dose-finding clinical trial, you have a small number of doses to test, and you hope find the one with the best response. Here “best” may mean most effective, least toxic, closest to a target toxicity, some combination of criteria, etc.

Since your goal is to find the best dose, it seems natural to compare dose-finding methods by how often they find the best dose.  This is what is most often done in the clinical trial literature. But this seemingly natural criterion is actually artificial.

Suppose a trial is testing doses of 100, 200, 300, and 400 milligrams of some new drug. Suppose further that on some scale of goodness, these doses rank 0.1, 0.2, 0.5, and 0.51. (Of course these goodness scores are unknown; the point of the trial is to estimate them. But you might make up some values for simulation, pretending with half your brain that these are the true values and pretending with the other half that you don’t know what they are.)

Now suppose you’re evaluating two clinical trial designs, running simulations to see how each performs. The first design picks the 400 mg dose, the best dose, 20% of the time and picks the 300 mg dose, the second best dose, 50% of the time. The second design picks each dose with equal probability. The latter design picks the best dose more often, but it picks a good dose less often.

In this scenario, the two largest doses are essentially equally good; it hardly matters how often a method distinguishes between them. The first method picks one of the two good doses 70% of the time while the second method picks one of the two good doses only 50% of the time.

This example was exaggerated to make a point: obviously it doesn’t matter how often a method can pick the better of two very similar doses, not when it very often picks a bad dose. But there are less obvious situations that are quantitatively different but qualitatively the same.

The goal is actually to find a good dose. Finding the absolute best dose is impossible. The most you could hope for is that a method finds with high probability the best of the four arbitrarily chosen doses under consideration. Maybe the best dose is 350 mg, 843 mg, or some other dose not under consideration.

A simple way to make evaluating dose-finding methods less arbitrary would be to estimate the benefit to patients. Finding the best dose is only a matter of curiosity in itself unless you consider how that information is used. Knowing the best dose is important because you want to treat future patients as effectively as you can. (And patients in the trial itself as well, if it is an adaptive trial.)

Suppose the measure of goodness in the scenario above is probability of successful treatment and that 1,000 patients will be treated at the dose level picked by the trial. Under the first design, there’s a 20% chance that 51% of the future patients will be treated successfully, and a 50% chance that 50% will be. The expected number of successful treatments from the two best doses is 352. Under the second design, the corresponding number is 252.5.

(To simplify the example above, I didn’t say how often the first design picks each of the two lowest doses. But the first design will result in at least 382 expected successes and the second design 327.5.)

You never know how many future patients will be treated according to the outcome of a clinical trial, but there must be some implicit estimate. If this estimate is zero, the trial is not worth conducting. In the example given here, the estimate of 1,000 future patients is irrelevant: the future patient horizon cancels out in a comparison of the two methods. The patient horizon matters when you want to include the benefit to patients in the trial itself. The patient horizon serves as a way to weigh the interests of current versus future patients, an ethically difficult comparison usually left implicit.

Related: Adaptive clinical trial design

 

“MTD” is misleading

Dose-finding trials of chemotherapy agents look for the MTD: maximum tolerated dose. The idea is to give patients as much chemotherapy as they can tolerate, hoping to do maximum damage to tumors without doing too much damage to patients.

But “maximum tolerated dose” implies a degree of personalization that rarely exists in clinical trials. Phase I chemotherapy trials don’t try to find the maximum dose that any particular patient can tolerate. They try to find a dose that is toxic to a certain percentage of the trial participants, say 30%. (This rate may seem high, but it’s typical. It’s not far from the toxicity rate implicit in the so-called 3+3 rule or from the explicit rate given in many CRM designs.)

It’s tempting to think of “30% toxicity rate” as meaning that each patient experiences a 30% toxic reaction. But that’s not what it means. It means that each patient has a 30% chance of a toxicity, however toxicity is defined in a particular trial. If toxicity were defined as kidney failure, for example, then 30% toxicity rate means that each patient has a 30% probability of kidney failure, not that they should expect a 30% reduction in kidney function.

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New development in cancer research scandal

My interest in the Anil Potti scandal started when my former colleagues could not reproduce the analysis in one of Potti’s papers. (Actually, they did reproduce the analysis, at great effort, in the sense of forensically determining the erroneous steps that were carried out.) Two years ago, the story was on 60 Minutes. The straw that broke the camel’s back was not bad science but résumé padding.

It looks like the story is a matter of fraud rather than sloppiness. This is unfortunate because sloppiness is much more pervasive than fraud, and this could have made a great case study of bad analysis. However, one could look at it as a case study in how good analysis (by the folks at MD Anderson) can uncover fraud.

Now there’s a new development in the Potti saga. The latest issue of The Cancer Letter contains letters by whistle-blower Bradford Perez who warned officials at Duke about problems with Potti’s research.

Robust in one sense, sensitive in another

When you sort data and look at which sample falls in a particular position, that’s called order statistics. For example, you might want to know the smallest, largest, or middle value.

Order statistics are robust in a sense. The median of a sample, for example, is a very robust measure of central tendency. If Bill Gates walks into a room with a large number of people, the mean wealth jumps tremendously but the median hardly budges.

But order statistics are not robust in this sense: the identity of the sample in any given position can be very sensitive to perturbation. Suppose a room has an odd number of people so that someone has the median wealth. When Bill Gates and Warren Buffett walk into the room later, the value of the median income may not change much, but the person corresponding to that income will change.

One way to evaluate machine learning algorithms is by how often they pick the right winner in some sense. For example, dose-finding algorithms are often evaluated on how often they pick the best dose from a set of doses being tested. This can be a terrible criteria, causing researchers to be mislead by a particular set of simulation scenarios. It’s more important how often an algorithm makes a good choice than how often it makes the best choice.

Suppose five drugs are being tested. Two are nearly equally effective, and three are much less effective. A good experimental design will lead to picking one of the two good drugs most of the time. But if the best drug is only slightly better than the next best, it’s too much to expect any design to pick the best drug with high probability. In this case it’s better to measure the expected utility of a decision rather than how often a design makes the best decision.