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Sample Size and Power: Phase 2 Trial Examples Part 3 — Transcript · YTtoTranscript

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Sample Size and Power: Phase 2 Trial Examples Part 3

NIH VideoCast · 2,170 words · 11 min read · EN

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Below is the complete, readable transcript of Sample Size and Power: Phase 2 Trial Examples Part 3 by NIH VideoCast on YouTube. Read the full text, copy any part you need, or generate a transcript for any video with our free tool.

Moving into Phase II, this is where we see our screening of new therapies. So, Phase II, they've gotten through Phase I. Not killing that many people, that's good. Phase II, I'm trying to still learn a lot about safety but learn a lot more about my doses. I'm not going to probably look at final efficacy,

but I might have some type of biomarker or surrogate outcome that I'm going to determine kind of a pseudo-efficacy that I'm going to power on. Our general idea in Phase II is, is it safe enough? And is there sufficient activity enough to bother to move this to Phase III? Move these still at large pivotal trials?

Again, if you look at the old definitions, they'll say, "Well, should we bother to move it to a randomized trial?" These days, almost every Phase II trial I work on is randomized. It is a rare exception that they're not randomized. Your issues of safety are still going to be really important here. And you have a fairly small number of patients, might be several hundred,

but it still depends -- like I don't see that many that are more than 100 people per arm, but sometimes that happens. Your problems in Phase II is that you are more likely to run into the unblinded or single blinded studies here, have all the problems that we talked about at the beginning of the course.

You have issues with placebo effect, investigator bias, regression to the mean. If you're running a single arm study, you're not really sure what caused those changes to happen. That's the reason that you see this big push. So, if you work in industry, you're one of these pharmaceutical or biotech companies, you're running non-randomized trials, you're running unblinded

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trials, you tend to move into Phase III, and you get burned. Everything that looked fabulous in Phase II does not pan out in Phase III. So, now I've just wasted sometimes billions of dollars running those Phase III trials. That's the reason that people are getting a lot tighter in Phase I and Phase II.

Because better to stop the product early, if it's not producing results. Same thing in academic medicine, folks. You're better to fail small, but be wise about your failures. And with that, then I'm going to talk to you about a non-randomized design. But actually, randomized designs have been built out of this. So, for Phase II, there's something called a two-stage optimal design.

This was developed out of NCI back I think in 1980s, if I remember right. And the idea is the premise for a lot of current Phase II designs. You want to seek to rule out an undesirably low response probability. So, let's say only 20 percent of people respond to treatment. I want to rule that out in favor of something that shows useful activity.

And let's say I've defined useful activity to be that 40 percent of my patients are stable or have improved outcomes. So, in oncology, they might run a single arm two-stage design using an optimal design and a predefined response definition. It is hard to define a response because then people want to tweak those numbers, right?

But, again, if we want to rule out a probability of 20 percent in favor of 40 percent, let's say, I set my Type I error at 0.1 and my Type II error at 0.1, all right? So, I'm willing to make -- I'm going to -- this is one of those cases where I set them equal to each other.

The idea being, I'm willing to tolerate a Type I error. And really, if there's something there, though, I want high power. I really want to see it. So, roughly, in this kind of more probability-based setting, I've got a 10 percent probability of accepting a poor agent and a 10 percent probability of rejecting a good agent.

So, if you'll look in Simon's paper -- and if it's not posted, I will ask Daniel to post it up in your class segment. He has this paper with all of these different kind of tradeoffs of these different probabilities and varying alpha and beta values. This is something that Steinberger invented and then built upon in the early

2000s for randomized trials. So, we're going to blow this up in a second. This table is Table 1 from Simon's paper. We have the difference in the probabilities being 20 percent. And we've got that we're going to reject the drug if the response rate falls through here. There is something called the optimal design, which is what Simon was trying to promote,

and one that it was already out in the literature called the minimax design. So, let's look up here. Our null is a response rate of 20 percent. We want to actually see 40 percent responders. So what do I do here? What I want to do is, initially, I am going to enroll 17 patients.

So, if you'd looked at the tiny footnotes, we're going to be in kind of this top row here -- or the bottom row, the bottom chunk. So, Stage 1, I enrolled 17 patients. If zero to three of them have a clinical response, I stop accrual. I assume it's not an effective agent. So, what I'm saying is there is no way I'm going to be able to rule out this 20 percent.

So, I'm just stopping early. But if four to 17 patients have a positive response, we can move on to the second stage. I'm going to accrue up to 37. So, I'm going to accrue 20 more patients. And if 10 of the 37 have a positive response -- or sorry, if 11 or more of the 37 have a positive response, then I think it's an active agent.

So, basically, I'm rejecting if I have three or fewer, then if I have 10 or fewer. What these other numbers were, are -- you know, here -- I have a chance on stopping early, right? It might be I stopped at 17. I feel like if 17 out of 17, I'm done realistically. But let's look at this.

So, if I do the standard sample size, under the null hypothesis, I have to enroll 26 patients. Probability, I'm going to end under the null that's 55 percent. It's pretty good. So, here it is in words for you what I just said. Under the design, if the null hypothesis is true, there's a 55 percent probability of early termination.

This is one reason we like phase designs, right? We get out early. It's not 100 percent sure, but 55 percent is better than 0 percent. On average in that two-stage optional design under the null, I enrolled 26 patients. If I use the one sample test of proportions, I need 34 patients. So, 34 is fewer than 37, but I don't have that chance to stop early.

And that's what I'm gaining in this two-stage design. If I use a two sample randomized test of proportions, I have 86 patients per group. And that's the reason this -- you have this lore of a single arm study. Why do I want to have two arms and randomized when I can get some information?

Maybe there's a problem that I have so many fewer patients, it takes me less time, and less money. This switch you have to balance as an investigator. Again, there are a lot of newer methods available. They all end up citing Simon. So, that's why Simon is here. So, let's talk about historical controls now.

And historical controls, let's say I've got a rare disease. I want to double their survival. Survival rate now is 15.7 months, and I want to with my new intervention double that median survival to 31 months. I'd say I'm going to have a Type I error of 0.05. I want a one tailed test.

And I want my power to be 80 percent. So, why one tailed? Basically, if they're dying, then this is going nowhere, right? So, if my survival is less, no, that's it. So, they -- and also, the reason that they went ahead and did a one tailed test is they said, "This is a rare disease, and we have to do everything we can to try

to have a reasonable test." And because they're like, "It's going nowhere," and they swore they're going to publish it either way, they're like, "Yeah, it's interesting," and it will be clear that this is wrong. So, they better went to a test. You need 60 patients for this. And we'll talk about how you figure this out.

About 30 in each of the two study arms. They come back and they say, "Okay, Dr. Johnson, I can accrue one per month." It was actually a different doctor they were talking to you, but he let me share the example. So, if you can get 60 patients, one per month, that's five years

to just enroll them in your study let alone follow them in the study. They needed 36 months of follow-up. So, that's an additional three years. So, now it's going to take me, and best case scenario, eight years from the time I start enrolling patients to when I stop collecting data. Yeah, that's a long time to wait for an answer.

Plus, realize it probably took you a couple of years to get this study up and running, it's going to take you a little bit of time to analyze and publish your data. So, they said, "Well, we want to use historical controls." We have a bunch of patients, they were controls in other studies,

and we want to use their data and put all patients that we have on the new therapy and compare them to the old patients. So, there was this old dataset. We had 35 patients. They've been treated in National Cancer Institute with this disease. Problem is they were initially treated from 1980 to 1999.

Of those 35 patients at the time they were looking at the records, three of them are still alive. Median survival time for the historical patients, so where they'd gotten the value from, was 15.7 months. And this is basically kind of like this observational study, right? But, you know, 1980, it's 2015 now. There's a lot different when we diagnose them, how

we diagnose them, what measurements you're taking, how you're recording it, how you decide that people are progressing, the treatments that we're giving them. Not just who treat their disease, but everything else, you know, to help their nausea and to help their anything. It's all different. So, you have to decide, do you use this data?

Is it really controlling for everything you need to control for? Does anybody else have data? Can you work with people around the world to do this protocol? How do you do it? So, these are the problems that come up in Phase II studies. You've got to constantly be weighing the advantages and disadvantages of your study designs.

You may have a single arm study that has a small sample size, that's good in some ways, but you've got no control information. You may have a two-stage design, and again, you might stop early with a small sample size, but if it's a single arm two-stage design, you've got no control. You might have the correct responder, non-responder rules, or you may not.

Are you sure that that difference is really what you care about? Can you make a binary distinction to really even define a responder? Historical controls. And again, it's great because you can use a small sample size, but you don't know how accurate that control group really is. You might decide to run multiple arms, sometimes randomized, sometimes not.

Sometimes I see people run like eight plus arm studies, but then they have no control arm. They're just comparing all the different doses to each other. I'm like, "That's great. But what if none of your doses work, or all your doses work the same?" Like, "You don't have a way to compare." So, if you're going to be running multiple arms, please

have something with some control in it, because it could be that every dose does something but it all does the same thing. The downside is it takes a lot more people. That said, I see more and more Phase I and Phase II studies enrolling hundreds of people, because they want to make sure what they're moving forward

into these final large pivotal trials is what they've got the best shot at. And that they'd better understand a lot of the safety information, the pharmacokinetics, and pharmacodynamics, and a lot of other information about potential efficacy in trials, especially in multiple different populations, because that's where we do our trials.