So, what are our types of randomized studies.
Parallel group is our classic study. I've mentioned that already a few times.
We have sequential trials. A whole list of other ones.
I'm going to go through all of these.
So, in a parallel group design, the idea is that I'm going to randomized patients
to one of x treatments.
So one of two treatments, one of four treatments, however many.
And I'm going to look for some response.
I'm going to measure them at the end of the study and just compare,
you know, how is everybody at the end of one year.
I might look at a change or a percent change from baseline.
So how do they change between baseline and one year.
I may look at repeated measures.
Maybe I actually take their blood pressure every four weeks, and I'm going to look
at the change in systolic blood pressure over time, and I want to look
at a curve of that information. That's called repeated measures.
Or I may look at a function of multiple measures.
If you think about it, body mass index,
BMI, it is in fact a function of your height and your weight.
So there are a lot of variations on parallel group designs.
We sometimes, but not always, do dosed titration with multiple study arms.
This is becoming more popular, especially if it's not a first in human product.
The idea is you want to titrate to the maximum tolerated dose
within a given subject.
Dose escalation studies with a control arm that you're simultaneously randomizing to.
People underestimate the importance of controls in really early research.
It used to be, you know, the old way is you only put everybody on intervention.
But especially when you have subjects that a lot of bad things
might happen to them, you may say, oh, one of my subjects died.
Well, if your subjects have a 50 percent mortality rate, it's kind of hard to tell
was it the treatment or the disease that caused them to die?
If you have a control arm, even in those very early studies, you can start to tease out
what are the differences in the adverse events?
What are the differences in the death rates, et cetera?
I know some of you all are making like ugly faces.
I'll be honest with you, like, this is real life in clinical research.
If you do interventional research, there's a very good chance you will kill people.
Not that you mean to, but you may in fact cause harm.
If we knew the answer, if we knew that people were or were not going to be harmed,
if we knew that something worked, we wouldn't need to do the research.
So, this is something that you have to kind of in
your gut make a decision if you're willing to do or not.
If you have thoughts about that, Steven Strauss' chapter in the book is a good one
to read. Dr.
Strauss died several years ago,
but he talks about a very personal journey that he had with one of the studies he did
where they found out very late in the process that in fact, they were causing harm.
And some of the people that worked on that study decided they had to leave research.
They had to leave medicine completely
because it was something that they just couldn't handle.
It's not an easy thing, but it's something to consider.
Now back to the design.
I mean, the whole goal of this course is to try to make
that you hopefully figure this out before you ever touch a human being, right?
We do not want to cause harm.
Not all dose escalation, dose
titration studies are randomized, but some of them are, more of them are now.
In sequential trials.
So sequential trials happen more in engineering,
but if you're doing device manufacturing, you may also do this.
You don't necessarily have a fixed sampled size or period that you're running the study.
This, of course, makes funders kind of scary.
IRBs go, "What?" So those are your institutional review
boards, the groups that approve human subjects research.
The idea with the sequential trial is that ends when one treatment shows
clear superiority or is highly unlikely any important difference is going to be seen.
So it kind of makes sense but you'll see this, like, computers, capacitors, et cetera,
but very special statistical design methods are needed when you do these trials.
One that you do see commonly in clinical research is group sequential trials.
So here kind of what we're going to talk about is type 1 error can be easily computed.
And you can't do that easily in the straight up sequential trials.
So these are very popular because these group sequential trials, you analyze your data
after a certain proportion
of the results, or the information from the trial is available.
There's early stopping, depending on how you set this up,
if one treatment arm is clearly superior, if it looks like there's futility,
so if you got to the end of the trial, you're still not going to have
significant results, you may as well stop now.
You may also still stop for adverse events.
So all trials should be monitored to see if they need to be stopped.
We'll talk about that in the second part of the course.
This takes a lot of really careful planning and statistical design work.
It's going to impact your sample size, so you have to roll the fact
that you're going to be analyzing your data before
the study is done into the planning of the study initially.
But this is an example that we had from a trial from NIAID, it's
actually a very old example, that was one of the first studies of
zidovudine, and it was done in pregnant women.
And so at the first interim analysis where one-third of the projected
infant infections happened, the data safety monitoring board saw this picture.
We're going to come back to this picture in the survival analysis lecture.
But this was a randomized trial, they randomized the mothers to either take
zidovudine or placebo,
and then they looked at the probability of transmission of HIV to the infants.
And you can see how kind of the study arms worked out.
So this is a Kaplan Meier curves that are on this screen
and then there's a p-value associated with it.
But a lot of work went in to trying to decide what should the interventions be.
What should the population be?
We knew zidovudine at the time was able to slow the progression of HIV in adults
with advanced disease, but this AIDS Clinical Trials
Group Protocol 076 was looking at safety and efficacy of zidovudine in preventing
transmission of HIV from infected but not necessarily advanced women to their babies.
So now I've got to figure out -- I've got a different population.
They're not necessarily advanced.
I've got to worry about not only mom.
I've got to worry about infant.
Because maybe they don't get HIV, but they have some other horrible problem
that happens to them.
You've got to think about what are the ramifications
of giving a drug to somebody, especially if it's a pregnant woman,
or if it's a male who might impregnant somebody.
Yeah, that's a little trick they forget to tell you about.
Everyone thinks about lactation and pregnancy,
and they forget that the guy plays a role in that pregnancy.
Anyway, so preventing HIV transmission, they had to power this study to detect
a 33 percent reduction in the transmission rate.
So the placebo rate, or the normal, natural history, I should say, rate of
transmission was 30 percent, and they wanted to drop it to 20 percent.
So this study they had planned was going to do accrual over five years.
They expected 15 percent dropouts.
Again, you expect that some of these folks you're not going to be able
to follow the entire time, for a variety of reasons.
Infants die for a lot of different reasons.
Sometimes also, you know, moms and infants they go somewhere else.
You can't track them.
You have to think about all this when you're trying to design your trial.
Also at that time, HIV testing -- not all that great.
So they had to figure out, like, what was in fact
a positive test in order to decide that someone had an event.
Another type of study's a crossover study.
So in a crossover study, let's say I have two treatments.
I will then have a two-period crossover.
Each patient acts as their own control.
The trick here is you need to eliminate crossover effects.
So if I'm going to have you all use an asthma inhaler
that then changes your lung structure in some way, changes your cells,
I probably am not going to wash that out, at least not for a while.
If I teach you meditation, I can't unteach it from you.
Somethings you cannot do in a crossover trial, but the idea
is that a lot of things you can.
So the women's alcohol study, we did a three eight-week dietary periods.
Each woman was randomized to the order in which they took in
different doses of alcohol.
So they either had 30 grams of alcohol a day,
which is the equivalent of about two drinks, 15 grams of alcohol a day,
so one drink, zero grams of alcohol a day, so they got an alcohol-free beverage.
Basically, they got orange juice and Everclear.
The order of the assignment of the three alcohol levels was random.
So that's the part that got randomized.
Each woman had each one of these three doses. Why?
Because we each have different set of hormones, different cardiovascular
risk factors, and we were trying to look at a lot of cancer risks.
Well, in
that case, kind of, it's better kind of do it inside a person, and their own diet,
and all of their own stuff that they are bringing outside of the alcohol.
We had washout periods.
And because this was such a long study, we actually varied the washout period.
So we had one group of people, the people literally packing the lunch at the USDA
and the dinners.
So every night they had a snack, and that snack included this beverage,
and they were told take it at the end, before you go to sleep,
do not drive, blah, blah, blah.
But, you know, differing washout periods --
and sometimes we always had the same washout period, but at least with alcohol,
we knew how long physiologically it took to get it out of the system.
And this was a double-blind study.
The investigators who were, you know, drawing their blood,
and checking their blood pressure three downings [spelled phonetically] a week.
They did not know what this person was on.
The women did not know what they were on.
Some of them said they thought that they knew that they were getting drunk at night.
And this was actually in a Washington Post article on this study.
And so after the study was over with,
the PI said can someone look back to see if she had been taking alcohol or not.
It turns out she'd only been in the placebo part of it at that point in time.
That's actually another trick I've learned.
Like, people who think like they're having all these huge side effects,
they think they know what study they're on, a lot of times you don't.
But anyway, same thing goes for the clinicians who are trying to
guess what study arm somebody's on.
So then you have these factorial designs.
So factorial designs,
each level of the factor, or treatment, or condition occurs with every other factor.
So this was a study that my NCI colleagues worked on,
it was in gastroenterology, where they randomized people.
You either got Selenium placebo, and Celecoxib placebo, or some combination.
So what you'll notice is kind of this bottom box is Celecoxib only.
And this top far box is Selenium only.
Down here in the bottom corner they're getting both Selenium and Celecoxib.
Now how does that work?
Well, it works if you don't think that Selenium
and Celecoxib interact with each other in particular with respect to your outcome.
So you'd
break up these factors and when you do the analysis, I compare
everybody in kind of this Selenium placebo
arm to everybody getting Selenium real, ignoring what Celecoxib they got.
And then I compare all the Celecoxib folks and the placebo Celecoxib
to Celecoxib real, ignoring their Selenium.
The problem is, a lot of times I do these, and then the investigators come back and say,
"So can you tell me if there is an interaction?" All right,
if you care about that interaction, if you expect it might exist,
you need to do a four arm study, not a --
so you can design -- it can look like this, but when you power this study,
you cannot power the study assuming that these two interventions
are independent of each other.
So you've got to make a decision.
Two two-arm studies or a four-arm study.
The MsFLASH also used a factorial design.
I liked this one because, okay,
there are a lot of things I don't like about the MsFLASH study.
I'll be honest.
But here you'll see that it's not evenly randomized
because what they did is they went a step farther.
They said we're not even going to compare yoga to aerobic exercise.
We're comparing aerobic exercise to usual activity.
We're comparing yoga to usual activity.
We're not going
to compare all three of these arms, but they have an unequal randomization
between the study groups in order to achieve the statistical power that they needed.
Then you run into thinks like incomplete, partial, or fractional factorial trials.
Depending on where you train, it is labeled one of these three.
Nutritional intervention trial's an example of this.
They had four different types of micronutrients that they were looking at.
And what they did is they didn't want to look at all possible interactions.
In fact, this study in the end,
I want to say had maybe like 30,000, 20,000 plus people in it.
And that was only looking at certain combinations.
But you will see groups that will do this, that will choose certain combinations
to look at, and you have to also make sure that you have
the ones in there that you need in order to do the analysis you care about.
The problem is, you know, in the end people want you to look at certain interactions
that you don't have in there, certain combinations you don't have.
So you do have to think pretty hard in advanced about what you want to leave out.
I'm going
to spend several minutes on adaptive designs because they're gaining a lot of popularity.
Here you have maybe two to eight different arms.
Sometimes it's dose ranging, sometimes not.
People think you have, and you'll see it in all these clinical journals,
if you do adaptive designs, you'll have a smaller overall sample size.
Yeah, sometimes.
Sometimes you have a larger overall sample size but at least, you know,
you're able to do it in one trial.
A lot of these have kind of a run-in period
and then you start analyzing data continuously or at fixed points.
But for any adaptive design, and there're like 30 plus different versions
of adaptive designs, you need to be clear.
What is being adapted?
So the number of people in each study arm?
Is it something about the randomization, like the characteristics of people?
Is it the invention themselves?
What is being adapted?
When are you going to adapt it?
And based on what evidence does this adaptation take place?
Who decides an adaptation is needed?
And how is it implemented?
So this is a slide from one of Paul Wakim's lectures
that he actually got from Paul Gallo, who's in the pharma working group.
Basically, the idea with adaptive designs is this is a clinical study design that uses
accumulating data
from your trial to decide how to modify aspects of that same trial as it continues.
But the trick is, you've got to do this in a way
that doesn't undermine the validity, integrity of the trial.
Now, if you look at my employer's work on this, we'll also say an adaptive
design is defined as a study that includes prospectively planned opportunities
for modification of one or more aspects of the study design and hypotheses
based on analysis of data, usually interim data, from subjects in the study.
So one of my studies, they wanted to do adaptive study.
We thought it was a good idea except then we looked and found out
they basically had to follow patients
for three years before they had any good information on their outcome.
They were going to enroll over a four-year period.
So the question was, what types of adaptations made sense?
Like maybe we could look early to decide in fact patients shouldn't finish the trial,
but we had to actually
get some of that long-term data in order to make that determination.
So you have to think about what adaptations make sense.
It doesn't always make sense to adapt your randomization.
It might make sense to stop early.
So you have adapted
randomizations, adapted dose findings where we may turn on and off different doses
based on the adverse events or other characteristics
that we're seeing, drop the loser or pick the winner.
Again, you have to be careful there's some really bad examples where, you know,
they made a decision to drop a study arm, but that arm only had one patient in it,
and it was the patient that was the sickest of everybody.
That's kind of a problem.
We also do these adaptive seamless phase II/phase III trials.
Biomarker adaptive trials.
So sometimes based on your biomarker,
we may put you in different study arms, or we may change your study arm.
We have group sequential methods.
So realistically, that group sequential
-- parallel design that I talked about first, is basically an adaptive trial.
We also do these sample size recalculations.
We'll talk about the variance and issues like that
and how you can use that to try to re-estimate sample size.
So a lot of people like adaptive trials, but this is not willy-nilly folks.
The rules have to be pre-specified in the protocol.
The changes are made by design. This is not ad hoc.
This is not because you see something and you want to make a little change.
This is not a way to fix a badly designed trial.
Stuffs going down the tubes, now you want to try to fix it,
you know, that's a salvage operation. It is not an adaptive design.
Adaptive designs require a lot of understanding.
They are hard to do for investigators, reviewers, DSMB members, journal editors.
Not all statisticians know how to do all of them.
There are a lot of advantages and disadvantages.
You actually -- while you have flexibility, it comes at a price.
You need a lot more quantification of statistical risk.
You have to understand a lot more information to actually plan these adaptations.
A lot of them happen and they happen based on statistical rules.
It's going to be following the data and make a change.
You don't actually make a decision that it should make a change.
That means you have to know well enough what might happen.
You also have these covariate imbalances.
So I mentioned
how the confounders aren't a problem unless you have an adaptive randomization.
This is part of your problem.
It's a lot more work upfront.
But they can be very useful if you have the information.
Your big negative for any trial, though, is that whenever you make a decision
to continue or to make a change, that information
about the study may be provided to investigators, the public, investigators.
When you have a data safety monitoring meeting, and decide to continue a trial,
it can change stock prices.
That is very sad, but it is very true, and a problem that we have today.
So enriched enrollment designs.
This is kind of a variant of your crossover or n-of-1 studies.
N-of-1 is when I take a patient, and I kind of do randomly assign
when I'm going to assign them, so it's like an expanded crossover study,
but within any given patient. In enrolled enrichment designs,
I try to identify potential responders to the treatment.
I enter those responders
into a second prospective comparison study, and people think this is great.
I have a better chance of a win except this is not generalizable
to your general patient population.
Sometimes, though, clinicians will tell me, well, it actually is.
I actually try my patients.
If they seem to be responding, we stay on the drug,
and if they don't seem to be responding, I switch their drug.
Well, again, you need to think about every clinical trial within large situations.
How are you going actually implement this therapy?
And how can you work that implementation process into your actual trial structure?
Results tend to not be generalizable
and you get this thing called regression to the mean.
So the problem when you try to enroll, let's say, I have a hot flash study,
and I want to enroll people that are having hot flashes in order
to see if I can decrease their number of hot flashes, right.
Problem is, like, I will get -- they'll be having 10 hot flashes a week.
I put them on the main study, I randomize them,
and like in my control group I'm seeing two hot flashes a week.
That's because a lot of times we enter trials when we are fairly sick.
And it's kind of a natural ebb and flow for a lot of parts of disease.
And so then we naturally go back to kind of a normal low
and now my people that are trying to analyze the data say, "Oh,
we don't have enough events." I also saw this happen in like, you know,
infectious disease studies.
Like, you see this happens in a lot of strange studies.
Herpes studies, they're having all these outbreaks, and now they have none.
Good for the patients, not good for my study investigator.
Group or cluster randomized studies.
We've got a unit of randomization that's not the individuals.
So normally when we randomize, we randomize the individuals in the study.
But if I want to randomize an entire school and give all the kids in that school
an intervention, if I'm going to randomize a community,
I'm going to vaccinate everybody in a community, for example.
If I'm going to change practice within a clinic
and then observe what happens to the individuals
who are patients in that clinic, or the providers in the clinic.
Then my unit of randomization is the school, or the community, or the clinic, it's
not the individuals inside of it.
Now this could be really important
because sometimes you are trying to make a change where, you know, I can't give
pamphlets of information in the waiting room to one person versus the other.
If they're all in the same waiting room, they can all pick up the pamphlets.
Sometimes you'll see providers saying, you know, it's very hard for me
to kind of change my treatment across different people when this is an open study.
So other times, also, like we were looking at charges for bed nets,
this was a group out of MIT, and they wanted to look at the impact
on infant malarial cases.
So everyone had said you need to charge for bed nets
so that people are feeling like they're empowered.
They have spent their money. They will use the bed nets.
And this couple of female economists were sitting around looking at what was going
and they're like, no.
I can't remember their names, but they gave a really great talk on this.
And so they actually randomized different clinics to have different pricing structures.
Some charged none, some charged different prices.
And then they looked to see how many bed nets got picked up or sold,
then how many got used, then how many got used appropriately, but overall
they said all the other economic analyses look at all those,
but what we care about is infant malarial cases.
So they looked to see what the infant malarial case count was.
In fact, people who buy a bed net are more likely to use it.
But so many more people picked up the free bed nets, that
that in fact was what lowered the infant malarial cases.
What they also did as they went and visited these different houses, is
they noticed like these bed nets
basically take up the entire structure and people were decorating them.
They also heard that one of the main reasons people didn't put them together is
they still didn't understand the instructions.
And to their credit, those investigators sat there with the instructions,
and tried to put together the bed net, and they couldn't figure it out.
So they came up with the equivalent -- if you know the store IKEA,
they kind of came up with these like IKEA picture instructions.
They tested the instructions with some folks, figured out how to help them understand it.
They also make prettier bed nets.
Because if this is your central fixture in the household, it helps to make it
pretty because people said they were more likely to use it that way.
So then they ran another study.
Pretty bed nets for free versus standard bed nets for free.
People like pretty bed nets. It lowers infant malarial cases.
So, you can test pretty much anything, you just have to find the place
to do it, and make sure it's a worthwhile question.