1

DEPARTMENT OF HEALTH AND HUMAN SERVICES

FOOD AND DRUG ADMINISTRATION

CENTER FOR DRUG EVALUATION AND RESEARCH

JOINT MEETING OF

THE ARTHRITIS ADVISORY COMMITTEE AND

THE DRUG SAFETY AND RISK MANAGEMENT

ADVISORY COMMITTEE

VOLUME III

Friday, February 18, 2005

8:07 a.m.

Hilton Gaithersburg

620 Perry Parkway

Gaithersburg, Maryland

P A R T I C I P A N T S

Alastair J. Wood, M.D., Chair

Arthritis Advisory Committee:

Allan Gibofsky, M.D., J.D.

Joan M. Bathon, M.D.

Dennis W. Boulware, M.D.

John J. Cush, M.D.

Gary Stuart Hoffman, M.D.

Norman T. Ilowite, M.D.

Susan M. Manzi, M.D., M.P.H.

Drug Safety and Risk Management Advisory Committee:

Peter A. Gross, M.D.

Stephanie Y. Crawford, Ph.D., M.P.H.

Ruth S. Day, Ph.D.

Curt D. Furberg, M.D., Ph.D.

Jacqueline S. Gardner, Ph.D., M.P.H.

Eric S. Holmboe, M.D.

Arthur A. Levin, M.P.H., Consumer Representative

Louis A. Morris, Ph.D.

Richard Platt, M.D., M.Sc.

Robyn S. Shapiro, J.D.

Annette Stemhagen, Dr.PH. Industry Representative

FDA Consultants:

Steven Abramson, M.D.

Ralph B. D'Agostino, Ph.D.

Robert H. Dworkin, Ph.D.

John T. Farrar, M.D.

Leona M. Malone, L.C.S.W., Patient Representative

Thomas Fleming, Ph.D.

Charles H. Hennekens, M.D.

Steven Nissen, M.D.

Emil Paganini, M.D., FACP, FRCP

Steven L. Shafer, M.D.

National Institutes of Health Participants

(Voting):

Richard O. Cannon, III, M.D.

Michael J. Domanski, M.D.

Lawrence Friedman, M.D.

P A R T I C I P A N T S (Continued)

Guest Speakers (Non-Voting):

Garret A. FitzGerald, M.D.

Ernest Hawk, M.D., M.P.H.

Bernard Levin, M.D.

FDA Participants:

Jonca Bull, M.D.

David Graham, M.D., M.P.H.

Brian Harvey, M.D.

John Jenkins, M.D., F.C.C.P.

Sandy Kweder, M.D.

Robert O'Neill, Ph.D.

Joel Schiffenbauer, M.D.

Paul Seligman, M.D.

Robert Temple, M.D.

Anne Trontell, M.D., M.P.H.

Lourdes Villalba, M.D.

James Witter, M.D., Ph.D.

Steve Galson, M.D.

Kimberly Littleton Topper, M.S., Executive

Secretary

C O N T E N T S

Call to Order:

Alastair J. Wood, M.D. 5

Conflict of Interest Statement:

Kimberly Littleton Topper, M.S. 5

Naproxen Investigator Presentation

Alzheimer Prevention Study: ADAPT

(Alzheimer's Disease Anti-Inflammatory

Prevention Trial):

Constantine Lyketsos, M.D. 14

Additional Background Presentations

Interpretation of Observed Differences

in the Frequency of Events When the

Number of Events is Small:

Milton Packer, M.D. 42

Clinical Trial Design and Patient Safety:

Future Directions for COX-2 Selective NSAIDS

Robert Temple, M.D. 95

Issues in Projecting Increased Risk of

Cardiovascular Events to the Exposed Population

Robert O'Neill, Ph.D. 109

Summary of Meeting Presentations:

Sharon Hertz, M.D. 132

Sponsor Responses 140

Advisory Committee Discussion of Questions 147

Question 1: 165

Question 2: 284

Question 3: 320

Question 4: 356

Question 5: 367

Question 6: 391

Question 8: 418

Question 7: 432

Meeting Wrap-up 438

P R O C E E D I N G S

Call to Order

DR. WOOD: Let's get started. This is our

third day and thanks to everybody for coming back.

We have obviously entertained you sufficiently.

Kimberly has a statement to read.

Conflict of Interest Statement

MS. TOPPER: The following announcement

addresses the issue of conflict of interest with

respect to this meeting and is made a part of the

record to preclude even the appearance of such.

Based on the agenda, it has been determined that

the topics of today's meeting are issues of broad

applicability and there are no products being

approved.

Unlike issues before a committee in which

a particular product is discussed, issues of

broader applicability involve many industry

sponsors in academic institutions. All special

government employees have been screened for their

financial interests as they may apply to the

general topics at hand.

To determine if an conflict of interest

existed, the agency has reviewed the agenda and all

relevant financial interests reported by the

meeting participants. The Food and Drug

Administration has granted general-matter waivers

to the special government employees participating

in this meeting who require a waiver under Title

18, United States Code, Section 208. A copy of the

waiver statements may be obtained by submitting a

written request to the agency's Freedom of

Information Office, Room 12A-30, of the Parklawn

Building.

Because general topics impact so many

entities, it is not practical to recite all

potential conflicts of interest as they apply to

each member, consultant and guest speaker. FDA

acknowledges that there may be some potential

conflicts of interest but, because of the general

nature of the discussions before the committee,

these potential conflicts are mitigated.

With respect to the FDA's invited industry

representatives, we would like to disclose that Dr.

Annette Stemhagen is participating in this meeting

as a non-voting industry representative on behalf

of regulated industry. Dr. Stemhagen's role on

this committee is to represent industry interests

in general and not any one particular company. Dr.

Stemhagen is Vice President of Strategic Develop

Services for Covance Periapproval Services, Inc.

In the event that the discussions involve

any other products or firms not already on the

agenda for which an FDA participant has a financial

interest, the participants' involvement and their

exclusion will be noted for the record.

With respect to all other participants, we

ask, in the interest of fairness, that they address

any current or previous financial involvement with

any firm whose product they may wish to comment

upon.

There is one administrative announcement.

Would you please make sure that you take your phone

calls outside. It is messing up with our audio and

we would really appreciate it. Thank you.

DR. WOOD: The other administrative thing

that the sound person has asked me to say is, to

the committee, try and remember to switch off your

microphones when you are not using them.

Apparently, it messes it up.

MR. LEVIN: Mr. Chairman?

DR. WOOD: Yes, Arthur?

MR. LEVIN: I wanted to express a concern

I have in terms of the agenda for today's meeting.

For those of us who have been at advisory committee

meetings before, we know that there is often a

tendency to sort of squeeze the most important part

of these advisory committee meetings which is the

discussion and answers to the questions and giving

directions to FDA.

My concern is that, given the lengthy

discussions we have had over the past two days and,

given the fact that this is last day, that we will

not have enough time to fully explore all of the

questions that have been raised over the last two

days and to give some definite direction to the FDA

as to how to pursue these issues.

So I would like to suggest to the group

that we might shorten the presentations, or

eliminate them entirely, in order to have adequate

time to fully discuss all of our concerns and

different points of view around the table. I think

it would be really unacceptable to leave here today

unable, because of a time constraint, to give

direction to the FDA on this issue.

DR. WOOD: Did you have any particular

people you wanted to eliminate? Or do you want to

pass me a note, privately?

MR. LEVIN: It may be something the

committee as a whole should decide.

DR. WOOD: Let me make a suggestion. I

think that is a reasonable approach. I am sure the

committee will want to hear the data from the ADAPT

study and we should hear that in its totality.

Milt Packer has come a long way so we should hear

from him, I think. Milt is always entertaining,

anyway.

Do we really need to hear from the two

Bobs?

DR. TEMPLE: I don't have any ego involved

in this. A fair amount of--some of what I am

talking about is about the adverse consequences of

blood-pressure elevation which I think I could

skip. So I could shorten it considerably. But you

guys decide. It is there for you to read if you

want.

DR. WOOD: Why don't you do this. Why

don't you distribute your talk to us.

DR. TEMPLE: I think it has been.

DR. WOOD: Right; I understand that. I

will take that as a given. And both of you make

whatever remarks you would like to make from your

seats there at the times that you are allotted, but

brief and pointed. And let's not revisit all the

things we have visited before.

DR. TEMPLE: That's fine.

DR. WOOD: Does that sound fair? Dr.

O'Neill?

DR. O'NEILL: Yes; that is fine.

DR. WOOD: That will save us some time.

So that is a good thought. In addition, we have

got Sharon Hertz's talk which, I notice, has

40-something slides here--45 slides--which is a lot

to get through in a few minutes. So I think, while

we are sort of working up to that, she may want to

look at that and decide what she really needs to

say. I mean, after all, it is very unusual for the

FDA to summarize the meeting for the committee,

which is partly what the committee is here to do, I

guess.

So let's make sure that she can finish

that taking the time she has been allotted for it

which is 30 minutes. She would be better to remove

some slides rather than rush through it, I think.

Having said all that, let's get to the

first presentation. Does anyone else have any

thoughts on that? Yes, Annette?

DR. STEMHAGEN: I would like to ask

whether the manufacturers could have just one or

two minutes to make some summary comments before we

start our deliberations after lunch.

DR. WOOD: Do they want to do that now?

Is that what you are asking?

DR. STEMHAGEN: No; I think after these

presentations.

DR. WOOD: Okay.

DR. STEMHAGEN: Thank you. I appreciate

it.

DR. WOOD: Let's have some discussion

amongst the committee.

DR. CUSH: What would be the purpose of

their having--they have had lots of time already to

present their data and had lots of mike time in the

back already.

DR. STEMHAGEN: Just in terms of the

deliberations that have gone on, there might be

some clarifying comments.

DR. CUSH: I think, if we have questions,

we can ask for clarifying comments. I think that

is what we--I would suggest--and I agree with

Arthur Levin in that we should get on to discussion

as quickly as possible.

DR. STEMHAGEN: I realize this is sort of

in contrast to try to shorten it. But I would like

to ask that that time be awarded.

DR. WOOD: Any other thoughts on that?

Let me get a sense of the committee. What is the

committee's pleasure about that? Yes?

DR. BOULWARE: I actually support that

recommendation, too, and would suggest you give

them a limited time, like you did with the public

comment where you will cut them off at two minutes,

so we know it will be limited. I would be

interested in the direction they plan to take. We

heard some startling news yesterday about the

possible remarketing of a product that they have

withdrawn.

DR. WOOD: Does anyone object to them

getting two minutes apart from Dr. Cush? Then, I

think, the answer on that is that that is fine.

Remind them that, in contrast to most of their

experiences in the past for senior managers, the

microphone will be cut off.

DR. STEMHAGEN: Thank you very much. I

think we saw evidence of that yesterday.

DR. WOOD: Right. So they got the

message; right? Okay. Let's move along to the

first speaker, Dr. Lyketsos.

Investigator Presentation

Alzheimer's Prevention Study: ADAPT

DR. LYKETSOS: Good morning, everyone. I

do not have slides. My name is Constantine

Lyketsos. I am a professor at Hopkins and I am

presenting here today on behalf of the ADAPT study,

Alzheimer's Disease Anti-inflammatory Prevention

Trial. I would like to thank the committee for

inviting us to present. I am here today with my

colleague, Steve Piantadosi, who is also on the

steering committee and will be available to answer

any questions that might come up later on as well.

I have a prepared statement that will be

distributed to the committee later on today. I

delivered it to the staff this morning as I was

arriving.

Before I get into the statement, I just

wanted to take a few moments to remind us of the

public-health importance of Alzheimer's disease to

somewhat set the context about how the ADAPT trial

has started specifically. Alzheimer's, as we all

know, is a major public-health problem. It is a

devastating disease, typically runs a ten-year

course of neurodegeneration affecting probably

close to 4 or 4-and-a-half million of our citizens

at present and the number is expected to rise given

the aging of the population of the next several

decades to approach, perhaps, 12 to 15 million,

based on current projections.

Because of the these public-health

numbers, there has been a very significant effort

in our field for the last several years to develop

preventive strategies for Alzheimer's disease

because, once neuronal degeneration has started,

the evidence that treatments work, so far, is very

weak.

These preventive strategies have centered

on several possible treatments but the most

supported by the observational literature have been

nonsteroidals with over 24 studies right now

including four prospective population studies

suggesting substantial reductions of risk of

Alzheimer's disease perhaps with risk ratios, in

some cases, as much as 0.4 or 0.5. So it is within

that context that ADAPT was started with the

support of the National Institute of Aging.

I will move now to reading the prepared

statement.

The steering committee of the ADAPT study

welcomes the opportunity to present the rationale

for its decision, on December 17, 2004, to suspend

the NSAID treatments in ADAPT. This presentation

is important because there is much public

misunderstanding about our decisions and their

rationale.

The ADAPT Steering Committee is deeply

committed to the safety of human subjects, even

more so in the context of prevention trials where

risks are typically not balanced by any promise of

tangible near-term benefit. In this notable way,

prevention trials differ from treatment trials

whose participants may hope for relief of symptoms

or improved outcomes in a condition already

diagnosed.

The risk:benefit balance in prevention

trials is even further removed from a comparison of

the benefits of a proven treatment with its

acknowledged risks. Because ADAPT has not quite

completed the process of auditing and tabulating

the trial's cardiovascular safety on the date of

suspension, we cannot, today, present the trial

safety results at the time of the decision to

suspend.

We defer that presentation to a

peer-reviewed publication planned for the near

future. For today, we note that, even with the

risk:benefit calculus of a prevention trial, these

data would not, in themselves, have led to our

decision to suspend either treatment. In reality,

those decisions were made in very unusual

circumstances. They reflected events external to

ADAPT that raised strong concerns about the

practicalities of continuing the treatments.

As the advisory committee probably knows,

ADAPT is a randomized, double-masked, multicenter

trial of celecoxib, 200 milligrams twice daily, or

naproxen sodium 220 milligrams twice daily versus

placebo for the primary prevention of Alzheimer's

dementia and for the prevention of age-related

cognitive decline which is, in many instances, a

prodrome of Alzheimer's disease.

ADAPT also provides an opportunity to

study the long-term safety of its treatments in a

healthy elderly population. Eligibility criteria

include an age of 70 years or older at enrollment

and a health history that excludes many of the

known risk factor for adverse events with NSAID

treatments; for example, we exclude those with

preexisting uncontrolled hypertension, anemia or a

history of gastrointestinal bleeding, perforation

or obstruction.

To provide independent recommendations

regarding continuation of the trial, the ADAPT

Treatment Effects Monitoring Committee, or TEMC,

which, I suppose, is our term for a DSMB, meets

twice a year. In response to emerging concerns

about cardiovascular risks with NSAIDs, membership

of the TEMC was recently expanded to include Dr.

Bruce Psaty, a physician with expertise in

evaluation of cardiovascular risks in clinical

trials.

As an additional safeguard for participant

safety, the ADAPT study officers and consultants

also conduct reviews of safety data at intervals

between TEMC meetings. Amid the emerging

controversy about the cardiovascular safety of

selective COX-2 inhibitors, the ADAPT study officer

had been relatively reassured by their periodic

reviews of the celecoxib safety data. The study

chair communicated this information in a telephone

conversation on 15 October 2004 with Dr. Sharon

Hertz at FDA.

As of December 17, 2004, the data of

suspension of treatments and enrollment in ADAPT,

we had enrolled 2,528 participants. Of these,

2,463 had been randomized before October 1 of '04

with some 20 months average duration of

observation. These participants contributed a

total of 3,888 person years of follow up to

analyses that were presented to the TEMC on

December 10, 2004.

Those analyses suggested a weak signal

suggesting increased risks of cardiovascular and

cerebrovascular events with naproxen. Reviewing

the data, however, we understood well the TEMC's

evident conclusion that this signal was not

sufficiently compelling or definitive to warrant a

recommendation to suspend the treatment or to

otherwise alter the protocol. This was on December

10, 2004.

Thus, the study officers were surprised on

December 17 by announcements that two trials of

celecoxib for the prevention of recurrent

adenomatous colon polyps had been suspended citing

increased cardiovascular risks with treatment in

one of these studies, the Adenoma Prevention with

Celecoxib trial, or APC. This news led to

extensive discussion among the steering committee

on that day centering on the following

considerations.

Number one; one arm of the APC trial had

used the same celecoxib dosing as ADAPT, 200

milligrams twice daily, but over a longer period of

time. News reports cited a relative risk of 2.5

for cardiac events in this arm of APC. Although

this risk was reported as only "marginally

significant," a greater cardiac-risk signal was

reported with the higher APC dosage of 400

milligrams twice daily.

Thus, we took seriously the possibility of

harm over time to ADAPT participants receiving

celecoxib. Especially in a prevention trial with

no strong prospects of immediate benefit, we had

strong misgivings about continuing celecoxib

treatments.

Knowing almost nothing at the time about

the particulars of the APC trial and, in light of

the apparent lack of risk with celecoxib in the

other prevention trial, we might have discounted

the APC data and continued celecoxib. To do so,

however, we would clearly have needed the

concurrence of the seven IRBs that oversee ADAPT.

These IRBs began almost immediately to question us

about implications of the APC results and seemed

likely to question a decision to continue.

Even if we had persuaded them to permit

continuation of celecoxib using a revised consent

process, we would surely be involved in lengthy

discussions with these IRBs. In the meantime, we

would be unable to offer much explanation to our

participants, thereby endangering the relationship

of trust that is vital to the success of long-term

trials.

Number three; as is common in long-term

trials, ADAPT was experiencing some difficulty with

adherence to treatments. This difficulty grew

following the withdrawal of rofecoxib and we

expected the announcement of the APC results to

exaggerate the problem further with scores of

participants stopping treatment, in effect, "voting

with their feet." This would erode statistical

power and increase the potential for bias in ADAPT.

Thus, even though the ADAPT safety data

did not, themselves, warrant suspension of

celecoxib treatments. There seemed little

practical choice but to do so.

We next confronted the dilemma of what to

do about naproxen and its placebo. As suggested

above, we regarded the accumulated naproxen safety

data as being somewhat more concerning than the

celecoxib safety data. Yet, they, also, were not

compelling. Although some post hoc data composites

barely reached statistical significance--these are

post hoc data composites barely reached statistical

significance for naproxen versus placebo, no

singular vascular event was clearly more frequent

with naproxen versus placebo.

Furthermore, vascular risks were not

expected with naproxen treatment. In fact, a

substantial body of prior data at the time had

suggested that naproxen offers some cardiovascular

protection. This lack of prior expectation cast

further doubt on the meaning of the naproxen data

in ADAPT which were vulnerable, in any case, to the

problem of multiple comparisons.

We could, therefore, have attempted to

have revised ADAPT to a two-armed trial of naproxen

versus placebo, instructing our participant to stop

taking their "white pills," as they are known in

the study, which are celecoxib and its placebo, but

continue to take their "blue pills," which contain

naproxen and its placebo.

However the dangers were several.

Participants might end up getting confused and

taking the wrong pills and many would stop taking

their treatments altogether. We faced an ethical

dilemma. The suspension of celecoxib and

continuation of naproxen would have created the

impression among participants and among the general

public that celecoxib was risky but naproxen was

"safe." At least based on the signals from the

ADAPT data, this impression would have been

misleading.

What would we then tell participants about

the risks with naproxen as we led through the

inevitable process of revised consent necessitated

by the protocol revision. Would the multiplicity

of IRBs even allow us to follow this course?

Finally, there was another risk to

consider. We began ADAPT expecting to see some

increase with naproxen in gastrointestinal bleeding

and other events. Even though we attempted to

reduce these excess G.I. risks by excluding

participants with prominent risk factors other than

age, the ADAPT data showed a notable increase in

G.I. bleeding with naproxen versus placebo.

Especially amid concerns that ADAPT was

exposing its participants to potential risks that

were immediate, while the trial's hoped-for

benefits lay in the future, the totality of the

above arguments lead the steering committee to

suspend both treatments and to also suspend

enrollment into ADAPT.

As noted above, we expect, within a few

weeks, to submit a scientific paper for peer review

and publication. The paper's focus will be on the

process and rationale underlying the decision to

suspend treatments and enrollment in ADAPT.

Because these decisions did rely, in some measure,

on the ADAPT safety data as of 10 December, the

paper will, also, disclose some of these data.

We are also cooperating with ongoing

efforts at the NIH to investigate the

cardiovascular and cerebrovascular risks of NSAIDs.

In addition, the NIA and the ADAPT Steering

Committee are committed to a further two years of

additional safety monitoring of our participants.

In preparation for a later, more

definitive discussion of the ADAPT safety data, we

plan to revisit a number of the adverse events to

collect additional information and then to submit

all information available now or later to a process

of expert adjudication. Depending on particulars,

the latter process will take months. In the nearer

term, we concur with the expert opinion that,

having taken these widely publicized decisions, the

steering committee must fulfill its obligation to

disclose its reasons for doing so based upon the

data available.

At the same time, we are intent that our

public presentation even of the current "working"

data must be at the highest attainable standards of

accuracy.

Thank you.

DR. WOOD: Thank you very much. Are there

questions directed to the speaker? Dr. Nissen?

DR. NISSEN: I fully understand your

rationale and I understand that the trial was

fundamentally stopped because of an issue of

futility. You didn't think that you could keep

people in the celecoxib arm. That is all well and

good. The problem that occurred here is that a

warning was issued on naproxen which had the effect

of being the medical equivalent of screaming "fire"

in a crowded auditorium.

All over the country, many of us got calls

from patients saying, "I want to stop my naproxen

because it causes a cardiovascular risk." I think,

just a comment here, that it would have been far

better to have announced that the trial was

suspended for futility rather than for hazard when

there was a non-statistically significant hazard.

So, one man's comment.

DR. WOOD: I agree with that. Any other

comments? Yes?

DR. FARRAR: I wonder if you could comment

on the G.I. bleed component since, obviously, one

of the deliberations we have to undertake is the

relative problems with G.I. bleed versus

cardiovascular risk. Certainly, that was known a

priori before starting the study.

As you commented very carefully, that

wasn't the only consideration. But, in a drug

trial where the outcome is unknown and the risk is

really fairly well known, I wondered how you

thought about that in terms of putting patients at

risk of something on the order of a few percentage

over the course of a five-year trial who might have

serious complications from the G.I. bleeding.

DR. LYKETSOS: I guess you are asking me a

human-subjects question.

DR. FARRAR: I am asking how, in the

design of the study, obviously the choice was made

to accept that risk for the unknown potential

benefit of reduction in Alzheimer's disease over

the course of the same trial. I am wondering if

you have any insights into how that decision was

made because, clearly, there are issues there about

the use of these drugs and their risks.

DR. LYKETSOS: Well, I am glad you are

asking the question. It certainly is an issue that

we have spent a lot of time discussing and which we

discussed with study sections, IRBs, at quite some

length and continue to discuss.

I think the fundamental point that I would

start with is where I started my presentation which

is the devastation that Alzheimer's disease brings

and the fact that all the study participants were

individuals who had a first-degree relative with

the disease and had, therefore, personal

experience.

In that context, we were very careful and

very clear with them about what we thought at the

time the known G.I. risks were so that, in the

process of consent, and that was revealed through

careful discussions in the consent process as well

as the consent form, the risk of G.I. bleed was

stated very clearly and that that, in some cases,

might lead to death.

So I think we felt that this was a

decision that our participants could make, given

that the risks were relatively small, and the risk

that they would develop Alzheimer's disease was

higher and that we felt they could make the

decision for themselves if they were willing to

take the risk:benefit calculus as we saw it.

DR. WOOD: Dr. Gibofsky?

DR. GIBOFSKY: I share Dr. Nissen's

concern about this effect of crying fire in a

crowded theater. Many of our patients called and

suggested that they were going to stop their

celecoxib because of the concerns that were raised

from ADAPT as well. But you raised a very

interesting concern that I confess I hadn't given

enough thought to and that is the difference

between a prevention trial and an outcome trial.

Much of our discussion here later today, I

suspect, is going to focus on what action should be

taken, if any, to restrict drugs based on treatment

from data on prevention trials. I would be very

curious to hear you expound on that a bit more.

DR. LYKETSOS: That is an interesting

question. Let me just, if I could, because there

have been three comments now--I just would like to

refer you to the early part of my statement where I

said the presentation is important because there is

much public misunderstanding about our decisions

and their rationale.

Several of you pointed out that there was

a cry of fire. I don't believe that that came from

the study.

DR. WOOD: We won't ask you to speculate

where it came from. There is certainly a view on

that.

DR. LYKETSOS: I am not sure where it came

from. But, to address the other issue, I must say

I have not given it much thought as to whether

prevention-trial safety data would generalize in

the way that you are thinking about it. So I will

defer on that because I think it would need a fair

bit more thought by people who are more expert in

that.

DR. WOOD: Dr. Fleming.

DR. FLEMING: It is my understanding, from

what you are saying, that the steering committee

was particularly influenced by the APC prior data

not by the internal data from ADAPT; i.e., there

were, from you were describing, some emerging

trends that, in my words, were in the unfavorable

direction but in the context of monitoring trials,

we know that one has to be extremely cautious, when

you are looking at data continually over time, not

to overinterpret emerging trends that can easily

ebb and flow.

So my understanding, from what you are

saying, is it wasn't that there were, at this

point, some emerging trends that happen to be in

the unfavorable direction on naproxen. Rather, it

was the external data on the APC trial for Celebrex

that was the driving issue behind the

recommendation.

DR. WOOD: Just to develop that question,

what I understood you to say was you hadn't passed

some stopping boundary; is that correct?

DR. LYKETSOS: I'm sorry? I didn't hear

the first--

DR. WOOD: You hadn't violated your

stopping rule, or whatever stopping rules, you had

for safety.

DR. LYKETSOS: I think that our TEMC, our

DSMB, had opined the week before with the same data

from within the trial that they felt that we should

continue. So it was interesting how the two events

were back-to-back.

DR. FLEMING: I would like to come to that

second. I am leading to that. But first I wanted

to make sure that I understood what was the nature

of the concern. Is my interpretation correct?

DR. LYKETSOS: I think so. Back to how I

put it, the issue really was one of practicalities

more than our internal data, is that we felt we

would have to talk to IRBs and participants and

tell them something about--

DR. FLEMING: Could I first understand

what your sense of the evidence was. I want to

discuss that first, versus the practicality.

DR. LYKETSOS: The sense of the study

evidence.

DR. FLEMING: The sense of the evidence

that was the basis for the decision in terms of

adverse effects. I have heard two things. One is

the naproxen, but that was not compelling evidence.

That was within the framework of emerging results

that could be by chance alone when you are

monitoring data frequently. But external APC data

was very influential to you. That is what I am

hearing. Is that correct?

DR. LYKETSOS: Well, in fact, we didn't

know all the details of the APC data, as I pointed

out. I think it was that plus the climate that had

been created by rofecoxib coming off the market,

the influence that that had to some extent on our

participants, then the widely publicized APC

results and the sense that, even though the data we

were seeing and that our TEMC the week before had

seen, did not compel us to stop treatment based on

our own data, that there was now a climate created

where, practically speaking, we had to stop and

take stock and get more information, et cetera.

So it was that sort of the decision. I

was a complicated decision and that is why it takes

a three-page statement to try and explain what went

through our minds.

DR. FLEMING: There may not have been, to

the steering committee at this time, access to data

on PRECEPT for celecoxib or to the etoricoxib, the

lumiracoxib, data on naproxen that were very

favorable, but you did have access to the VIGOR

data which was very reassuring for naproxen and you

had evidence from the CLASS trial and some other

data from Celebrex.

I am perplexed that you would look at the

totality of these data and say that the results

were conclusive in terms of at least not being able

to provide information to the IRBs and to the

patients and caregivers in the trial representing

the totality of the data when your data-monitoring

committee had looked at the totality of the

evidence for benefit to risk.

On a data-monitoring committee, I have

always argued, don't just show me the safety data,

even if we are just looking at early assessments

for safety. It always has to be benefit to risk.

Even though, as you are pointing out, this wasn't a

therapeutic setting, prevention trials also provide

major opportunity for benefit. Preventing major

diseases is also a very significant benefit.

My understanding is your data-monitoring

committee, in looking at the data, looking at the

benefit as well as the risk, indicated the study

should continue. How did the steering committee

judge, without access to ongoing data, that benefit

to risk couldn't be sufficiently favorable and that

a notification to the investigators, to the

patients and to the IRBs, that the monitoring

committee has carefully looked at benefit and risk

and that the totality of the data is beyond the APC

trial when you are looking at Celebrex and

naproxen? Why wasn't that strategy pursued?

DR. LYKETSOS: First, as I pointed out in

my statement, some members of the steering

committee did have access to the data that the DSMB

had seen. That is the first point. The second

point is, as you point out and as I think this

whole discussion points out, is these are very

difficult judgment calls. They have to take into

account evidence but also practical aspects of

continuing to conduct this sort of a prevention

trial in this sort of a population.

I think it was the judgment call, and I

can tell you, there was substantial discussion

around this when we had the steering committee

meeting, about these very issues. It was the

collective judgement at the time that this was the

right thing to do, given the various issues that I

have articulated in my statement.

DR. FLEMING: I will just pursue one more.

I am dismayed to hear the steering committee, some

steering committee members, had access to the data.

That is also a violation of the principles of

monitoring trials. It should have been in the sole

possession of the data-monitoring committee.

I am also distressed because I am not

hearing that monitoring committee was front and

center in terms of having these issues brought back

to it for reassessment. So, to me, what I am

hearing raises very significant concerns about

putting at risk the integrity of studies with

prejudgments using only access to partial external

information.

DR. WOOD: There was one other thing,

though, at least the word on the street was, and

you sort of mentioned that as well, I understood

there was a very large number of dropouts from the

trial after the Vioxx withdrawal and others and

that one of the perceptions was it was no longer

possible to continue the trial. Is that true?

DR. LYKETSOS: Let me clarify that. The

adherence had been declining on an annual basis

even before rofecoxib was withdrawn from the

market. So adherence was perceived as an issue in

that we felt that now there were data about one of

the study drugs and that that would further erode

adherence. We did not see a huge erosion in

adherence with rofecoxib, specifically, but there

had already been an erosion that was concerning and

we anticipated a further erosion.

DR. WOOD: Right. But the question for

this committee that Dr. Fleming is pursuing

vigorously, and I agree with him, is that the

announcement that you all made--the announcement,

as it was picked up--maybe I should put it like

that--was that this trial was being stopped for a

safety signal.

What I heard in your statement and what I

hear from you now is that the trial was being

stopped for operational problems in the trial and

the safety signal was a convenient moment at which

to do that. But you had operational difficulties.

That is a very different interpretation and a very

different interpretation for the public and

patients.

Is that what you are hearing, Tom?

DR. FLEMING: It certainly appears to be.

It is part of what is concerning to me.

DR. LYKETSOS: I think my statement should

speak for itself. In terms of what the data were,

as I have pointed out, they will be submitted very

soon so that you can judge for yourselves.

DR. WOOD: Okay. Any other questions?

Sorry; Dr. Farrar. I beg your pardon. Dr. Farrar,

go ahead.

DR. FARRAR: I think, actually, that this

study provide some vitally important information

with regards to our consideration of the entire

class of drugs; namely, the NSAIDs. I would like

to just read on sentence from the statement.

It said, "Although some post hoc data

composites barely reached statistical significance

for naproxen versus placebo." Now, clearly, this

discussion would be much clearer after the

presentation of the data, a careful review of the

data. But Dr. Fleming noted that, in the VIGOR

study, there was some reassurance about naproxen.

I would like to just question that.

What is very clear in the VIGOR study is

that naproxen was safer than rofecoxib. But it

does not comment at all with regards to the

potential risk compared to placebo. In fact, I was

surprised when I heard the statement by Dr. Fleming

because, in fact, I have assumed, based on all the

data that we have, that every NSAID will not fare

well against a placebo.

I think that this data, and probably will

be supported by the publication although I don't

want to try and foresee the future, but my guess is

that naproxen will not fare particularly well

against placebo in terms of its cardiovascular

safety. I think we need to be able to accept the

fact that all of them have some risk with regards

to cerebrovascular disease and this study is likely

to provide the data to support that.

DR. WOOD: Dr. Nissen?

DR. NISSEN: I don't want to belabor this

because we have got a lot more to discuss today,

but I think it is extremely important that, as a

medical community, we learn from this episode. In

the kind of media frenzy that was going on during

that period of time, this announcement, this

warning that was issued on a national basis about

naproxen, was inappropriate, led to some panic

amongst the public and we simply can't do business

this way.

We can't operate in this kind of a

fashion. I would urge any of the individuals who

were involved in the decision to issue a warning to

go back and look at what happened and try to ensure

that we don't do this sort of thing again, because

once this gets picked up by the media, it passes

through generations of people and becomes the topic

of extensive discussion and may lead patients who

don't have the ability that we have around this

table to filter data--they don't understand

data-safety and monitoring boards. They don't

understand stopping rules. And it caused a panic

that was unnecessary and it shouldn't have

happened, and I hope it doesn't happen again.

DR. WOOD: Thanks very much. Let's move

on to next speaker, Dr. Packer.

Additional Background Presentations

Interpretation of Observed Differences in the

Frequency of Events When the Number

of Events is Small

DR. PACKER: Thank you, Alastair, members

of the advisory committee, FDA, ladies and

gentlemen. Today I have been invited by FDA to

address a specific question which is how should be

interpret differences in the observed frequency of

events in a clinical trial when the number of

events is small.

Let me just say arbitrarily that I will

define, for purposes of today, what I mean by a

small number of events and that would have provided

less than 70 percent power to have detected a true

treatment difference assuming an effect size

similar to that generally encountered in clinical

research.

This is just a thought. Just suppose you

do a trial for a noncardiovascular indication and

you note that there are 13 major adverse

cardiovascular events in the placebo group and 33

such events in the drug-treatment group. How

should this difference be interpreted?

Many would simply perform a statistical

test, derive the p-value, and get excited if the

p-value were less than some arbitrary value such as

0.05. In this example, the p-value of 0.002 would

suggest, to some, that this difference between 13

and 33 in a trial of about 3,000 patients, would

have been observed only two times out of 1,000, an

effect unlikely to have been due to the play of

chance.

However, before getting excited, we should

remember that p-values must be interpreted in some

context. P-values are most easily interpreted when

they refer to predefined primary endpoints in

trials adequately powered, more than 80, 90 percent

power, to detect differences between treatments.

However, even under such circumstances, p-values

are not necessarily reproducible.

Bob O'Neill and others have made the point

that, if a p-value in the trial is 0.05, the

likelihood of seeing 0.05 in a second identical

trial is only about 50 percent. It is only when

the p-value in the first study is 0.001 that the

likelihood of seeing 0.05 or less in the second

identical trial is at least 90 percent.

These calculations are the basis of the

frequent FDA guidance that, to demonstrate

persuasive evidence for efficacy, a sponsor needs

to provide two trials with 0.05 or less or one

trial with a very, very small p-value.

But what if the event was not the primary

endpoint in the study? What, in fact, if the event

was not even precisely defined before the start of

the trial? What if the trial was not adequately

powered to detect a treatment difference for the

endpoint? What does a p-value mean under these

circumstances?

Unfortunately, this happens quite

frequently in clinical trials under a variety of

circumstances. But it is particularly true in the

analysis of adverse events. So lets make a list of

things to worry about when using p-values to

compare the frequency of adverse events in a

clinical trial.

First, there are literally hundreds of

adverse events in a clinical trial and, therefore,

there are hundreds of possible comparisons that can

be made. Now, this is classically referred to as

the multiple comparisons problem. For example, if

a typical large-scale clinical trial yields as many

of 500 individual terms describing adverse events

and if a p-value were calculated for each pairwise

comparison, one would, of course, by chance alone,

expect about 5 percent of the terms, or about 25

events, at a p-value of 0.05 or less and 1 percent

of the terms are about 5 events to have a p-value

of 0.01 or less.

The second issue in interpreting

comparison of frequency of adverse events is the

fact that adverse events are spontaneous

nonadjudicated reports. Now, adverse events are

reported at the discretion of the investigator and

then translated into standardized terms. There is

little uniformity on how an event is identified,

defined or reported and this uncertainty increases

when the event is in a field remote from the

investigator's focus.

Now, some of you may believe that you can

fix this problem by carrying out blinded

adjudication of events after the fact.

Unfortunately, the rules guiding post hoc

adjudication are inevitably influenced by the

knowledge that a treatment difference has been

seen. In fact, any bar set by a post hoc process,

is capable of magnifying or diluting an effect.

For example, if you set very strict

criteria, a committee could reduce the number of

events and, therefore, reduce statistical power.

By setting very loose criteria, the committee can

include many questionable events and reduce the

magnitude of a treatment difference.

To make things more complicated,

adjudication committees do not generally examine

individuals who did not report an event to make

sure they didn't have an event.

The third issue in interpreting

comparisons of frequencies is that some signals are

apparently only if adverse events are grouped

together. Now, that is not much of a problem if

the difference is fairly straightforward and

focuses on one single event. But things can become

a little bit more complicated if the analysis

requires a combining event and combining trends

across two or more events in order to reach some

magical level of statistical significance.

Now, the problem is that these groupings

are frequently constructed after the fact, making

it possible to include only events that showed the

trend the investigator is interested in. For

example, if an investigator believed the drug

increased the risk of a major cardiovascular event,

he or she might first look at myocardial infarction

and stroke, but, finding little difference here, he

or she might be tempted to look at other related

events; for example, not seeing a difference in

myocardial infarction, an investigator might be

tempted to broaden the definition of a myocardial

ischemic event to include sudden death or unstable

angina if the differences between the groups

supported some predetermined judgment.

Similarly, not seeing a difference in

stroke, an investigator might be tempted to broaden

the definition to include a TIA. But the

possibilities of grouping is very, very large and

the possibilities of finding something, if you want

to be creative, are also quite large, even though

these differences may be related to the play of

chance.

As a result, the definition of grouping

may vary from study to study. Now, some

investigators try to fix this problem by setting up

a uniform definition to be used across all studies.

But when the definition is developed after a

concern has been raised, those creating the

definition have frequently already looked at the

data or have communicated with those who have

looked at the data, and know either consciously or

subconsciously what kind of definition is required

to capture the events of interest.

The fourth, and what I want to focus on

the most in my presentation, is the issue of

interpreting comparisons of frequency of adverse

events because the number of adverse events is

small and, because they are small, they result in

extremely imprecise estimates.

Now, you may think that investigators

generally understand the difficulties of analyzing

small numbers of events. For example, most

investigators know that, when the number of events

is small, the lack of an observed difference does

not rule out the existence of a true difference.

We have been taught that this should be apparent by

looking at the confidence interval and, as you can

see here, the confidence interval is very wide and

includes the possibility of benefit and harm.

So investigators, basically, consider

these kind of data to be inconclusive. But what is

generally not appreciated is that, when the number

of events is small, the confidence interval is

necessarily so wide that it may not truly represent

the range of values that would include the true

effect of the drug. As a result, even the finding

of an observed difference does not necessarily

prove the existence of a true difference.

To illustrate this point, this slide shows

the effect size and confidence intervals required

to reach statistical significance in a hypothetical

trial of 3,000 patients assuming a range from a

very small to a very large number of events.

Now, assuming the trial shows a

statistically significant effect--that means that

we are only going to look at this if a p-value,

let's say, is less than 0.05--the smaller the

number of events, the larger must be the treatment

effect in order for this effect to be statistically

significant and the wider the confidence intervals

have to be.

Put it another way, if the number of

events is small, the trial will show a significant

difference only if the treatment effect is very

large and the estimate of the effect is very

imprecise.

Unfortunately, when you look at adverse

events in a trial, the number of events will always

be small. This is because the trial, as you know,

was designed to provide enough data to examine the

primary endpoint, the trial produces a very precise

estimate of, but it is not powered to look at any

other analyses and, therefore, at the end of the

trial, you get generally a less precise estimate of

the secondary endpoint and an extremely imprecise

estimate of any specific adverse event.

Now, you may ask, what is wrong with an

imprecise estimate? Well, imprecise estimates are

fine if the intent is to withhold judgement until

more data are collected to make the estimates more

precise. But imprecise estimates are problematic

if the intent is to stop and reach a conclusion.

That is because, when calculated in the

usual manner, p-values and 95 percent confidence

intervals are most easily interpreted in the

context of a completed experiment. Unfortunately,

the adverse-event data generated in a typical trial

is not the result of a completed experiment. In

fact, viewed from the amount of data needed for a

precise estimate, the adverse-event data in a

single study only represents a snapshot of an

ongoing experiment to characterize the safety of

the drug.

As a result, performing an analysis of

adverse-event data is akin to performing an interim

analysis of primary endpoint data in an ongoing

clinical trial. Now, this is important because we

know a fair amount of how to interpret interim

analyses in a clinical trial and here I really must

apologize to Tom Fleming because what I am going to

review here very quickly is borrowed heavily from

his extensive work in this area.

But it is really important to think about

small numbers of adverse events as an interim look

on a global effort to characterize the safety of a

drug.

Now, as you know, when you look at interim

analyses in a clinical trial, one plots the

treatment difference represented by a z-score

against the amount of information that we have, and

that is generally represented by the fraction of

expected events.

We start the trial at zero effect and zero

information. At the end of each interim analysis,

we add a point until we get to get to the end of

the study. Now, if we have assigned an alpha of

0.05 to the endpoint, we want to make sure that we

evaluate the treatment difference seen at the end

of the trial against an alpha of about 0.05 which

generally corresponds to a z-score of about 2.0.

Now, some might think, naively, that,

during the course of a study, the observed

difference between treatments will be so

predictable that we would observe a linear march

between the start of the study and the end of the

trial. But know that when the amount of data is

small, things tend to bounce around a lot, so much

so that early results can be very misleading.

It is sort of like the situation of trying

to predict the results of an election when only 1

percent of the precincts have been reported and

they are not even representative. So, as a result,

if we got excited about any difference in z-score

more 2.0 early in the trial, we would be getting

excited about effects that were not likely to be

seen or sustained if we had more data even though a

z-score of 2.0 would normally correspond to a

p-value of less than 0.05.

In fact, the smaller the amount of data,

the more things can bounce around a lot, the more

it is likely that what we will be seeing will be

due to the play of chance. Therefore, to prevent

investigators from reaching a conclusion when the

estimates are imprecise, statisticians,

particularly Tom, have recommended that

investigators refrain from getting excited about

nominally significant z-scores when the amount of

data is scarce.

Specifically, they have proposed that

boundaries must be crossed before we can feel

comfortable that an effect seen early is likely to

be present at the end of an experiment.

Now, Tom, in particular, has proposed a

curvilinear boundary like this. There are many

other boundaries that have been performed by

others. But this is very, very commonly used in

the United States. This represents a boundary with

an alpha of 0.05 for a primary endpoint. It sort

of looks like this. Because it is curvilinear, to

be significant at the 0.05 level, the treatment

difference must be extreme when the amount of

information is small as would be the case early in

the study.

However, as the trial proceeds, treatment

differences required to conclude that there is an

effect at the 0.05 level decreases and become

closer and closer to a z-score of about 2.0 at the

end of the study.

Now, this is a very different thought

process and a very different approach than getting

excited about a p-value less than 0.05 no matter

when you observed it during the study. For

example, a z-score of 2.5--that is right

here--would be meaningful if seen at the end of the

study but it wouldn't be considered significant if

seen early in the study even though the nominal

p-value at this time is less than 0.05.

Now, if the number of events is small, the

difference would need to be far more extreme--say,

a z-score up here--to be meaningful at the 0.05

level.

Here is a specific example. This is an

old cardiovascular trial. This is the Coronary

Drug Project. It was carried out more than 30

years ago. It included a comparison of clofibrate,

a lipid-lowering drug, and placebo on coronary

events. At four separate times during the study,

the difference in favor of clofibrate was

statistically significant at a nominal p of 0.05 or

less. But, at the end of the trial, there was no

difference between placebo and clofibrate. The

difference seen early in the trial was related to

the imprecision inherent when analyzing small

numbers of events.

In fact, if a boundary had been used in

this study, at no time during the trial would the

treatment effect have crossed the boundary and led

to the conclusion that clofibrate was better than

placebo.

Now, let me say this kind of fluctuation

early in a study is very, very common. There are

even examples that at treatment has been associated

with a nominally significant adverse effect which

later was reversed during the course of the trial

and became statistically significant at the end of

the study.

Now, I should mention that the boundary

that I have shown you is a boundary with an alpha

of 0.05. This means, when the boundary is crossed,

the p-value for the treatment effect is less than

0.05 not less than the nominal p-value that

corresponds to the disease score that allowed the

boundary to be crossed.

Now, for each p-value or each alpha, there

is a separate boundary. The requirement for

strength of evidence as it becomes more stringent,

the boundary is shifted upward and to the right.

You might ask why am I going through all

this. Because analyzing data derived in an

underpowered trial raises the same concerns as

analyzing data derived from an underpowered interim

analysis in an adequately powered study.

The cardiovascular field is replete with

examples of how misleading small numbers of events

can be. Let me give you a few examples. For

example, in an early pilot trial, the ACE/NEP

inhibitor, Omapatrilat, reduced the risk of a major

cardiovascular event by 47 percent when compared

with an ACE inhibitor. As you can see, the

confidence intervals are extremely wide because the

analysis here was based on only 39 events.

Later, a definitive trial was carried out

that recorded nearly 1900 events. There was no

difference between Omapatrilat and the comparator

ACE inhibitor on the same endpoint in the same

population.

Here is another example. In an early

pilot trial, amlodipine reduced the risk of a major

cardiovascular event by 45 percent, small p-value

but wide confidence intervals. Later, in a

definitive trial which recorded four times as many

events, there was no effect of amlodipine on the

same endpoint in the same population using the same

investigators.

There are even examples when the effect

seen in a pilot trial was reversed when the

definitive study was carried out. Two examples.

In two pilot trials, both in heart failure, one

with the drug Vesnarinone, one with the drug

Losartan, both drugs significantly reduced the risk

of death--not a minor endpoint; death--by 50 to 60

percent. But these benefits were seen in trials

that were each recorded fewer than 50 events and

thus produced treatment estimates with extremely

wide confidence intervals.

When both drugs were reevaluated in

definitive trials that recorded ten times as many

events, both drugs were associated with increased

risks of death, in one case, significant at the

less than 0.05 level.

Now, notice that the confidence intervals

of the treatment effect in the definitive trials do

not overlap with the confidence intervals of the

treatment effect in the early pilot studies. So

here we have an effect, two examples, of an

underpowered trial that showed a significant

benefit whereas the definitively powered study

showed significant harm.

Here is another example. This is a

meta-analysis of a small number of trials looking

at the effect of magnesium in acute myocardial

infarction. A meta-analysis of a number of studies

showed intravenous magnesium associated with the

striking reduction in mortality, a 55 percent

reduction in risk of death, but wide confidence

intervals, a very small p-value, in a fairly large

study.

This effect appeared to be reinforced

smaller treatment effect but wide confidence

intervals and then, subsequently, in a definitive

trial that recorded 4,000 deaths, there was a

nearly significant adverse event of magnesium on

the same endpoint in the same population.

Now, again, please note that the

confidence intervals of the treatment estimate in

this definitive study do not overlap at all, with

the confidence intervals of the estimates in the

earlier moderately sized study, and not at all in

the meta-analysis. Again, this is really a

reflection of the imprecision inherent in looking

at small numbers of events.

Let me give you one final example because

it actually deals with an adverse effect. In an

early pilot trial with extended-release

metoprolol--this is a study that looked at a very

small number of events, about 20 events, showed a

three-fold increase in the risk of hospitalization

of heart failure in the metoprolol group compared

with the placebo group. Look at the confidence

intervals here. They go from about Washington to

California, very, however, nominally significant

treatment effect.

When this trial was replicated in a

similar population with exactly the same drug,

exactly the same formulation, exactly the same

dose, there was now a reduction in the frequency of

hospitalization for heart failure. Let me just

emphasize, this was recorded as an adverse event in

this earlier trial.

So what have we learned from all this?

Well, a couple of thoughts. To achieve statistical

significance in an underpowered analysis, the

effect size must be extreme and the estimate must

be imprecise. Yet the more extreme the effect, the

more imprecise the estimate, the less likely it

will be reproduced in a definitive trial. That is

why I think, of all the things that we can worry

about in looking at adverse events, the most

worrisome is the imprecision inherent in the

analysis of small numbers of events.

Let me just close with a few final

thoughts. You might ask, based on all of this,

what should we do. Well, I think the first step,

perhaps the most important first step, is to

develop an approach to analyzing data in trials

with small numbers of events which actually

accurately reflects the true imprecision of the

treatment effect estimate and its statistical

significance.

Let me just emphasize one thing, and I

just want to put this as a proposal. In no way,

would I propose this as a definitive solution but,

to get the discussion going, this might be an

interesting first way of thinking about this.

The conventional way of comparing small

numbers of events is to calculate 95 percent

confidence intervals followed by the derivation of

the p-value. However, the conventional calculation

of the confidence intervals incorporates into it a

z-score that the investigator designates as the

target value for statistical significance. For

example, most statisticians, in calculating a

confidence interval, would simply use a z-score of

about 2.0.

And they would do that because that is the

critical value for the z-score at the end of an

adequately powered trial with an alpha of 0.05. So

what they would do is they would take this z-score

and they will use it to calculate the confidence

interval. What a lot of people, I think, fail to

realize is that this z-score is not the critical

value for decision making if one looks early in the

same experiment.

Early in that experiment, the critical

value for a z-score should be determined by the

interim monitoring boundary appropriate for the

information content, not the z-score at end of the

study.

Now, if one uses the boundary z-score in

the calculation of the 95 percent confidence

intervals, the confidence intervals here will be

much, much wider resulting in a p-value that will

no longer be statistically significant. Now this

is important because everyone talks about p-values

at these meetings. I showed you these data before.

Conventionally calculated, the p-value would be

0.002 meaning the likelihood of chance alone being

2 in 1000.

Well, if, in fact, if one recognized that

the data here really result in a very imprecise

estimate and one incorporates the thinking process

of an O'Brien-Fleming boundary into this, as a

reflection of this imprecision, then the confidence

intervals now truly reflect the imprecision in the

estimate and now the p-value is a lot interesting

than it was before.

Now, the use of boundary-adjusted

confidence intervals would, I think, appropriately

describe the great uncertainty inherent in the

analysis of small-numbers events, hopefully

markedly reducing the false-positive error rate.

In spite of using a boundary-adjusted

confidence interval, adverse effects that are known

to be characteristic of specific drugs would

generally remain statistically significant.

However, this approach, and it is just a thought

experiment, would not provide a way to interpret

trends observed in imprecise data.

So, lastly, let me just conclude with some

thoughts about what we should do with worrisome

trends in imprecise data. The first thing we could

do is believe in those that are biologically

plausible. However, we need to be very careful

here. Everyone knows physicians can always be

relied on to propose a biological mechanism to

explain the validity of an unexpected and

potentially preposterous finding simply because it

happens to have an interested p-value. Anyone who

doesn't believe this, you know, I would be happy to

show you overwhelming evidence that this is the

case.

Second, is we could look for confirmatory

evidence in other studies reminding that we

shouldn't be selective. But, even if every study

showed the same trend, how would you know that you

had enough evidence to reach a conclusion? Some

have proposed doing a cumulative meta-analysis in

which each trial is considered to represent an

interim analysis on the way to a final judgement.

Indeed, Salim Yusef has proposed that, as

each trial is added to the meta-analysis, that one

use interim monitoring boundaries to interpret this

cumulative meta-analysis. This has, certainly, a

considerable amount of appeal.

Let me just emphasize. Salim has, in

fact, underscored the fact that the conditions here

are not identical those that exist for a true

interim analysis. In the case of a true interim

analysis, we generally know that the types of

patients in studies are similar at all observation

points. Here it is different.

In the case of a cumulative meta-analysis,

the types of patients in studies differ across the

various trials. So, as a result, Salim has

proposed that, when reaching a conclusion based on

data that has been combined across trials, that a

boundary more strict than 0.05 be used.

Now, he has specifically outlined the

importance of this using the example of intravenous

magnesium. I showed you the data on intravenous

magnesium in myocardial infarction. When the early

trials with magnesium were carried out, the z-score

of greater than 2.0 was crossed early. As the

cumulative evidence occurred, the initial boundary

of 0.05 was crossed.

But then a large study, when added to the

other cumulative analyses, brought this treatment

effect down to a 0 level. So Salim, and others, in

fact, have emphasized that, when you are using a

meta-analysis approach and using intra-monitoring

boundaries, that maybe one should require a p-value

of less than 0.05 or even, perhaps, a small

p-value.

Let me say that most of the effects the

committee has seen over the past two days would not

come even close to meeting these criteria.

Now, some of you may say, why not avoid

all of this uncertainty and simply carry out an

adequately powered definitive trial with the

adverse event as the primary endpoint. Is this

crazy? No; it is not crazy at all. Sponsors

pursue encouraging trends. Most are disappointed,

but they will pursue them. Sponsors, therefore,

should have an obligation to pursue discouraging

trends realizing that most of them probably won't

be confirmed either.

On a definitive trial can address

ascertainment and classification biases as well as

concerns about multiplicity of comparisons and

imprecision of the data. However, can we really

expect sponsors to pursue every adverse trend?

There are some obvious limitations to doing this.

Furthermore, if you could decide which adverse

trend you wanted to pursue, how easy would it be to

carry out the trial intended to definitively

evaluate an increased risk of an adverse effect?

Can you imagine the consent forms for the

IRBs for such a study? Some may say that we are

being too stringent here, the that criteria of

raising a safety concern need not be as stringent

as the criteria for establishing efficacy. But I

am not so sure that the criteria for establishing

efficacy and safety should be that different.

As a rule, we are very strict in reaching

conclusions about efficacy because saying that

there is a benefit when there is none means that

millions will be treated unnecessarily and subject

to side effects and cost. Now, although some might

advocate being less strict in reaching conclusions

about safety, please remember; saying that there is

an adverse effect when there is none means that

millions will be deprived of an effective

treatment.

In conclusion, the findings of controlled

trials are most easily interpreted when they

represent the principal intent of the study. A

non-principle finding is subject to many

interpretive difficulties many of which we have

reviewed; ascertainment biases, inflated

false-positive rates due to multiplicity of

comparisons and, the one I have emphasized the

most, the imprecision of estimates inherent in the

analysis of small numbers.

I think FDA, industry and academia remain

in a quandary as to how to respond in a responsible

fashion to observe differences in the reported

frequency of adverse events. Let me just

emphasize, my presentation shouldn't be construed

as favoring one particular side in all the

discussions that have occurred. In my view,

regardless of one's position, it is critical to

understand the limitations of what we know and to

resist the temptation to reach conclusions before

we are justified to do so.

I think only by recognizing our ignorance

will we be able to take the first step towards

developing a rational approach that is in the

interest of all patients.

Thank you. I will be happy to answer any

questions.

DR. WOOD: Dr. D'Agostino?

DR. D'AGOSTINO: Thank you very much,

Milt. I have a couple of questions that I think, I

hope, are relevant to our deliberations. In terms

of your sense of large and the idea of chasing

after a safety event and making more out of it than

one should, we have a study approved where there

was a serious up-front prestated deliberation to

make sure they had good ascertainment and

adjudication of cardiovascular events, and they

come up with 45 versus 25 events, carefully

collected.

I am struck by that's being small, but I

am also struck by the carefulness in which it was

done, say, as opposed to the APD where they did an

interim analysis that has those problems. Could

you comment on, say, the approved study?

DR. PACKER: I think that, when you have

incomplete data, as you would if you have

small-numbers events, you need to be a lot more

careful about the thinking process. That doesn't

mean you can't make judgments. It doesn't mean you

can't incorporate a set of principles that would

guide decision making by looking at the totality of

the evidence and bringing to the process what you

inherently believe. I think that is what the

committee needs to do today.

What I really wanted to address, however,

is how hard this is and that the normal

reliance--as you know, clinical investigators,

because they don't understand p-values, rely on

them. What I am trying to do is to explain that,

in fact, we are less certain about what we know

here than we, perhaps, should be.

DR. D'AGOSTINO: But that is on the

approved, studies, it was reasonable, too.

DR. PACKER: I think you need to take that

in the totality of the carefulness in which it was

done, the prospective nature of it. But, remember,

in all the examples that I showed you, the trend

seemed sometimes very striking trends in early

pilot trials that were prespecified, adjudicated

endpoints but, because they were small-number

events with very imprecise estimates, the

definitive trial was non-confirmatory.

So just because it is up-front and

predefined--

DR. D'AGOSTINO: That is my question, yes.

That is my question. You still end up with small

numbers. Let me have just a couple of other

questions. The second question is really bothering

me very much in terms of how we would recommend

trials. If you decide--if the group decides and

suggests to the FDA that there should be more

trials, more randomized clinical trials, the

sponsors are, then, going to have to go back and

say, well, they are going to set up a trial saying

the null hypothesis that the relative risk is 1.0

versus the relative risk is not 1.0.

Now, the best thing a sponsor can do is to

run a very sloppy study and they will accept that

null hypothesis because the confidence intervals

will so wide and they will contain 1.0. The

alternative is to sort of do a noninferiority type

idea that you end up the study, you end up with the

confidence interval, and that confidence interval

has to be below something like 1.3.

Do you have advice for us if you did this

sort of second approach? We are dealing with rates

like 1 percent. Could we live with a 1.3 relative

risk that you rule out, a 1.3 relative risk?

People may be dying if you do that. So how do you

respond to that?

DR. PACKER: I wish I knew the answer to

that. I think that it depends on the type of

adverse reaction. It depends on the particular

drug. It depends on the vulnerability of the

patient population. All of these need to be

factored together with the actual feasibility of

doing the study.

The one thing I would say is that one

learns very little by doing a lousy trial. So,

doing a good trial is the only way to get a

reasonable answer or reasonable estimate of the

answer.

DR. D'AGOSTINO: Just one more. I will

make it quick. In these trials, in many of these

trials, people just won't stay in the trial. Can

you give us some advice on how to deal with the

drop-out--now, there are rules that you could say,

the individual wants to leave, has decided to leave

because the blood pressure is building up or

because of G.I. problems building up.

To say, we are only going to look at that

individual for 14 more days after they leave, to

me, is a problem because if the blood pressure is

building up, they may be on their way and it may

take two or three months before they get an M.I.

and so forth. So you have got the sort of

dropouts, terminations, that are part of the

protocol but you also have the individuals who just

stop coming. And they could be substantial. So,

any advice to us?

DR. PACKER: Gee, as you know, when we do

trials for superiority, the effort that we put into

adherence is extreme. We really want people to

stay on treatment and we organize the trials to do

everything we can to ethically and reasonably

maintain adherence.

I take your point that, if the trial were

a noninferiority trial, it is possible that the

investigators and sponsor might be less motivated

recognizing that poor adherence works in their

favor. I think that there needs to be a reasonable

effort--I mean, you can maintain adherence in most

trials if you really, really want to.

DR. D'AGOSTINO: Thank you.

DR. WOOD: I suspect we are not going to

solve that problem today. Dr. Shapiro?

MS. SHAPIRO: Just a comment on your

comment. We all know, of course, that the Federal

Regulations require that participants be allowed to

withdraw and not be badgered into staying. But

what I really wanted to talk about was your

observations about how it is wrong to suggest that

we should not chase safety quite as rigorously

because we will, then, deprive ourselves and others

of information and access to effective treatment.

I don't think it is as simplistic as that,

in that, when we are looking at potential harm or

safety problems, we have to look not only at

likelihood that it exists but prevalence and

severity.

So I think that your response to that

approach has to take account of those factors as

well.

DR. PACKER: Let me try to reframe my

response. You can't isolate benefit from risk.

The judgment as to whether a drug should be used on

an individual basis or on a population basis has to

be the relative value of benefit to risk. You may

decide that you don't even want to pursue a safety

trend in a non-fatal event when you know the drug

prolongs life. That would be a very reasonable

judgment.

On the other hand, you might want to

vigorously pursue a very serious safety is in a

drug for a symptomatic or cosmetic condition. So

the risk-to-benefit relationship is the one that

has to be vigorously defined.

MS. SHAPIRO: Right. I am sure you will

agree with this; you also have to factor in

prevalence of the condition and likely use of that

drug in the population.

DR. PACKER: That's right. But it is

always--it is risk to benefit. The goal here is

not to say that the risk-to-benefit relationship

can be altered, simply because you want to

emphasize one part or another, has to be in the

context of the clinical problem and looked at from

the patient point of view.

DR. WOOD: Dr. Cush?

DR. CUSH: I have two questions. One, I

need some education. You were frequently referring

to very wide confidence intervals where it didn't

seem so wide. It was only, like, 0.3 and 0.4

where, obviously, when it ranged from 1.0 to 8.0,

that is very wide. But you used those terms in

both situations. Could you explain the differences

there?

DR. PACKER: Actually, I have used "wide"

to refer to extremely wide, moderately wide and

wide.

DR. CUSH: And narrow would be--

DR. PACKER: Narrow is less than wide.

DR. CUSH: Okay.

DR. PACKER: Let me try. All the examples

that I showed you that I characterized as wide

truly reflected estimates that had a high degree of

uncertainty associated with it. On the benefit

side, benefits that range from an 80 percent

reduction in risk on the high side to a 20 percent

reduction in risk--remember, and I guess I should

emphasize this and I guess Tom would reinforce this

dramatically, the concept of how these curves

looked like in terms of the width is not

symmetrical on both sides of 1.0. The lowest you

can go below 1.0 is 0. So wide confidence

intervals below 1.0 can be 0.2 to 0.8. Those would

be wide confidence intervals. There is no limit

for estimates greater than 1.0, so you can have 1.0

to 24 on the adverse side of this. So you have to

sort of think about what is wide differently when

you are looking at estimates below 1.0 than when

you are looking at estimates above 1.0. Maybe that

would be helpful.

DR. CUSH: That does help. Secondly, you

have told us that when we are dealing with

low-numbers adverse events and that being very

imprecise and hard to make conclusions from, is it

even less valid or even greater error to, then,

take that data derived in one situation, like in an

Alzheimer's trial, and then try to generalize that

to the general population?

DR. PACKER: But we do that all the time.

There is a general sense that efficacy is not

extrapolatable across diseases but safety that is

not disease-specific is extrapolatable.

Let me put it this way. If we didn't do

that, the problem that I put forward would be

really impossible, really impossible. So I

actually feel comfortable extrapolating safety data

across indications as long as the safety item is

not disease-specific.

DR. WOOD: Dr. Shafer?

DR. SHAFER: Thanks. That was actually a

very informative presentation and I can confirm the

distance from Washington to California.

There are really two questions here that I

think we need to bifurcate. One of them involves

the scientific question of getting at the truth,

whatever that is. I appreciate everything you say

and, prior to a drug being approved, at least

ideally, there would be adequate time and resources

to do exactly what you are proposing.

But there is a second question which is

how to inform clinical and regulatory decision

making based on imprecise information following

approval because, in that setting, a daily decision

is being made by patients and their physicians as

to whether or not they need to take the drug.

One question about how to approach these

sorts of imprecise data when, in fact, a daily

decision is occurring, is can you take the

confidence bounds for both the risk and the benefit

and integrate those over the public-health hazard

and the public-health benefit to try to incorporate

the entire--both the point estimates but also the

uncertainty about them into the regulatory

decision-making process?

DR. PACKER: Oh, wow. Just a couple of

comments. One, the precision of the estimates on

efficacy is almost always more precise, much more

precise, than the estimates on safety. So you have

this very precise estimate on efficacy. You have

this very imprecise estimate, in general, on

safety. And you try to sort of integrate them and

you have to now weigh them because it could be that

the efficacy thing you are looking at is really

important and the safety is sort of not very

important. Or it could be other way around, the

efficacy is sort of very small--the efficacy is

small, but the safety is a big risk.

DR. SHAFER: That is exactly the question.

DR. PACKER: You might think that someone

in the world might be clever to create a

statistical model that would allow that to take

place. I am actually much more comfortable with

people doing that than statistical models doing

that. Somehow, people have the ability to

integrate all of this, especially a group of people

have an ability to integrate this, much better than

any mathematical model.

I would be very uncomfortable if someone

were actually to propose a mathematical model that

replaced the human, very important human, element

here.

DR. WOOD: Dr. Farrar.

DR. FARRAR: Every example that I have

seen to date in looking at the risks in

overinterpreting data seem to go from being a

positive study to a negative study. I wonder about

the other way around and whether there are any

inherent differences in thinking about it the other

way around, the bottom line being that if you have

ten studies that show no safety issue with a

well-measured process, whether you can then say,

well, maybe the 11th study is going to show it

somehow.

DR. PACKER: I think you need to find out

how much information there is in each study, how

easily or how appropriate it is to combine the data

across the studies to determine how precise the

estimates, after you have collected and integrated

all of the data, and put that into a judgement as

to how much data you actually need to be confident

about the precision of the estimate.

So there isn't a uniform way of thinking

about. It is not like you will know it when you

see it. There is some guidance, some mathematical

guidance, that needs to be incorporated into the

thinking process.

DR. WOOD: Dr. Domanski.

DR. DOMANSKI: You know, I am not nearly

as sophisticated, really, Milton, as you are about

this sort of thing nor about some of the people in

the room, but I am a little bit concerned about

some of the examples. I will give you one. I

don't think ISIS 4 was a definitive trial of

magnesium, because I know something about that. We

did the MAGIC study which was a very large study.

Like ISIS 4, it was negative, but ISIS 4

was substantially different methodologically in

terms of when that was given. I think that example

actually, to be honest, is fairly misleading as a

result. I think it is an example of a stopped

clock is right twice a day. But, yeah; it came out

right.

But I a worried if that is the basis for

this--that kind of thing is the basis for this

discussion across more of the landscape.

DR. PACKER: Let me emphasize, Mike, that

I knew that if I picked one study and gave you an

example of one st that I would be at great risk

because everyone knows something about these

studies more than what I know about these studies

although some of the studies I actually mentioned

were studies I was personally involved with and

think that I know a little more about them.

So I just wanted to--I would not

overemphasize--and, in fact, one might

appropriately underemphasize--the magnesium

example. But the other examples, time and time and

time and time again. It is just like reaching

conclusions during a very early part of a study

based on interim monitoring. When you have small

numbers of events, the estimates are very imprecise

and may not reflect what happens at the end of a

complete experiment. That is just a general

principle.

I take your point about ISIS 4 but the

number of examples here is just overwhelming.

DR. WOOD: It is important, Milton, to

remember, we have replication for two of these

drugs and these safety signals here. So it is not

just single studies.

Dr. Furberg.

DR. FURBERG: Milton, I think that was a

great presentation. I think, for balance, it would

be nice if you can have examples showing the other

side, how trends in smaller studies were confirmed

in definitive trials. And I know plenty of those.

DR. PACKER: Oh, yes.

DR. FURBERG: That was never discussed.

You are painting a dark picture saying you can't

trust smaller studies. You are right. You never

know where you are going to end up and you need to

be careful. But don't say that you can't rely on

those.

DR. WOOD: I was actually on the advisory

committee that turned down Vesnarinone, that looked

at that study. There were lots of issues that came

up at that time that led us to do that. So it

wasn't just that there was a study that was

compelling and that people went with that.

Dr. Nissen?

DR. PACKER: Curt, let me just say that--I

think your point is very, very important. What I

have not done is shown many, many examples of

interim monitoring in trials where the early

results were reflective of the endpoint. I have

not shown a whole host, probably more than I could

think of, of all of the pilot trials where the

initial trends encouraged someone to pursue it and

that the second study was, in fact, very

confirmatory.

Let me just make my point clear. It is

just not as reliable as we think it is. It is not

that it is worthless. I do not want to say that.

If I have implied that, then I do not want to imply

that. I just want to say that the risk of error

early when you have small-number events is much,

much greater than when you have a much more precise

estimate at the end of the trial.

My plea here is that when you don't know,

the best thing you can do is say, "I don't know."

And that is my only plea.

DR. WOOD: Milt, when you have two trials

that replicate one another, with a p-value of less

than 0.05, if that was an efficacy endpoint, we

would approve on the basis of that; correct?

DR. PACKER: That's right.

DR. WOOD: But you are telling us that,

when it is a safety endpoint, we should not act on

that. I think it is counterintuitive.

DR. PACKER: No, no, no.

DR. WOOD: Hang on. That seems to me

counterintuitive. We have, for two of these drugs,

two randomized trials that replicate the outcome.

In three of the four trials, the outcome was

predefined, adjudicated and so on. That is about

as good as any drug that has been approved on the

U.S. market that I can think of.

DR. PACKER: Let me just add one

dimension, Alastair, to the thinking process and

that is that when you have a p less than 0.05 on

two trials, on the primary endpoint because it is

efficacy, you have two trials that were designed

for the endpoint and have fairly narrow confidence

intervals and precise estimates.

That is not the same concept as having a p

less than 0.05 on two imprecise estimates which are

combined together.

DR. WOOD: No; I understand that very

well. I think we all do. The issue here is both

of the second trials--both of the second

trials--were designed to test the safety issue that

was in the first trial even though they were

efficacy studies. So it is not like they were just

two trials that fell on the ground from Mars that

arrived with something. These were designed, at

least according to the sponsors, to check for that

outcome.

So I think you are overselling the point a

bit.

Let's move on. Dr. Jenkins?

DR. JENKINS: I found the presentation

very interesting and I wanted to probe a little bit

further on the APPROVe study because that is the

one that I think we were feeling very comfortable

with the finding in APPROVe. Yet, I went back to

Merck's presentation, and their prospective plan

was actually to combine three studies that were

going to be placebo versus rofecoxib in three

different populations.

Their plan was to have 25,000 patients to

evaluate the cardiovascular signal. Now, in

APPROVe, presumably, they had stopping rules that

the Data Safety Monitoring Committee saw an extreme

effect that met those criteria so they stopped the

study. But I am just interested in hearing your

thoughts about how should we interpret APPROVe

where the stopping rule is met for an individual

study when the prespecified plan was to have three

studies combined for 25,000 patients.

DR. PACKER: Gee, I must say that I am

delighted to have everyone ask me the hard

questions for this afternoon. I sort of think that

this is what this committee has to do. I only

wanted to add a dimension to the thinking process

here. I don't come with any answers on how to put

all of the data together. All of the points on how

to synthesize these data, I am very comfortable

with the human process of doing so as long as the

human process incorporates an understanding of how

difficult and imprecise this is and the fact that,

in the past, although it has led to predictions

that came true, it also led to predictions that did

not come true.

DR. JENKINS: I think, more specifically,

the point I was trying to get you to comment on is

not the overall interpretation of the rofecoxib

data but the fact that there was a plan for 25,000

patients in three studies. What I am trying to

understand is how should we, then, interpret a

finding from one of those three studies where an

interim analysis crossed the stopping boundary and

met the criteria for stopping the study. What

weight should we give to that finding in that

single study?

DR. PACKER: I don't think there is a

precise answer to that. Any time you deviate from

your preplanned attack on the conduct of analysis

of a trial, you weaken, to varying degrees, the

precision of the estimate and the confidence you

have in the data that you are looking at.

DR. WOOD: Dr. Nissen?

DR. NISSEN: Milt, there is an additional

subtlety here. Let me see if I can drill down with

you on it. What we have here is a class of drugs

where we have multiple trials within the class. So

what we are asked to do is not necessarily, in some

respects, for each individual drug, say, well, do

we have replication or not.

But if we take the position that this is a

class effect, then we have got four, or perhaps,

five trials. This came up once before. It was

kind of controversial. I think you may have been

on the committee at the time when we had the

angiotensin-receptor blockers for renal protection.

What the two companies did with two different drugs

is they stipulated that the other could use the

data from the other company's trials as supportive.

So the reason that this is really much

harder is that we have a lot of trials here. We

may not have reached all the evidence in an

individual drug, but we have trials across the

class of drugs. I wonder if you have any thoughts

about this because it is obviously a difference

between studying a single agent and studying a

class of agents.

DR. PACKER: I think that, Steve--I mean,

that is why the process works best when there are

human beings involved in the thinking process.

There is no predetermined sense that one should

bring to the process--that you confine the analysis

only to one drug. What you should allow yourself

to do is look at the data with one drug, look at

the data with drugs that you think are related.

If there are data that you think are in a

drug that really isn't related, you might want to

analyze that separately or do it both ways to see

if it is consistent. There is no statistical

formula that can guide the very important human

process here.

My major point is that the precision that

most clinical investigators think exists here isn't

as precise as we think it is. But that doesn't

mean that you--and Curt would emphasize this--that

doesn't mean that you can't put together your own

picture of the totality of the data and bring to it

a sense of whether it reaches some critical level

of concern.

In the absence of precision, you have got

to do that. But don't forget inherently that the

data are imprecise.

DR. WOOD: Curt, do you want to say

something else? No. Then let's move on. The next

speaker is Bob Temple who we are going to confine

to his seat.

DR. TEMPLE: Alastair, I have a question.

What am I supposed to do about my slides? Can

someone show them for me? I will delete many of

them.

DR. WOOD: Okay. You can come up here if

you do it quickly.

DR. TEMPLE: I don't care where I'm from.

I really don't.

DR. WOOD: Then Kimberly will work the

slides for you.

DR. TEMPLE: Okay; if Kimberly will do

that.

Issues in Projecting Increased Risk of

Cardiovascular Events to the Exposed Population

DR. TEMPLE: I was not in any way trying

to address the main issues the committee is

grappling which is about what to do about these

drugs. But it seems to me you can't help noticing

that there is some data we would all like to have

that we don't have and that is what I was trying to

address.

Obviously, the main thing we are worried

about is the effect of the COX-2-selective NSAIDs

on cardiovascular outcomes, notably death, stroke

and heart attack. But are particularly interested

in the single drug effects, whether they are all

the same. We are interested in whether we are

looking at true class effects of differences.

We also can't help noticing there is not a

lot of long-term data on the nonselective NSAIDs

and, of course, has been pointed repeatedly, some

of them are sort of selective anyway.

There is major interest in possible

differences in the subpopulations that might be a

different risks. I think there are mechanistic

considerations, how much of this is really likely

to be platelets and could there be a blood-pressure

effect. The importance of that, to me, is that it

is not quite clear what to do about platelet

effects, but, conceivably, you could manage a

blood-pressure effect if that was a problem.

There is a lot of importance and interest

in the dose and dose interval. And it is important

to think about how long studies have to be to

detect these things. Obviously, some of trials

seem to have shown things in a matter of seven or

eight months. There is some suggestion that some

of the effects need much longer to detect.

Skip the next one.

With respect to cardiovascular effects,

the main question is whether everything is really

answered. You know, there are lots of studies, as

Alastair was pointing out. They are not perfectly

consistent, maybe, but there are a number of

studies with a number of drugs that seem to be

showing the same thing.

I guess, to me, they don't seem entirely

consistent. There are a number of possible reasons

for that. One is that there really are differences

between drugs, or at least between doses. Another

is that even the best controlled studies sometimes

give different answers. Another is that small

effects are difficult to evaluate in epidemiologic

and even controlled studies. Then the last is that

the effects may be population-dependent. That has

been discussed.

So it does seem to me there is more to

learn. Skip the next. We all know that. Platelet

effects.

One of the things that seems important to

pin down and I don't think it has been pinned down

yet is the possibility that blood pressure is a

significant part of all this, that there is some

impression that Vioxx has bigger blood-pressure

effects than the other drugs, but I don't think

there is what we would call adequate data on the

effects of all these.

By adequate data, I mean data that gives

you information about the effect of drug over the

entire dosing interval, that has pinned down dose

response and that has pinned down the effect of

different dosing intervals. There is an

impression, though, that these drugs can reverse

the effect of other anti-hypertensives, perhaps,

especially, ones that work through the renal and

angiotensin system. They seem to have, at least

some of them, an effect on blood pressure generally

and then there are isolated reports of hypertension

in trials reported as adverse reactions, clearly

more common in the treated groups.

I have a bunch of slides showing that

elevated blood pressure is bad for you. You can

deduce that from epidemiologic effects, from a

mountain of clinical studies. The most recent

study that of interest, which I will not

describe--keep going--in detail is a study that

Steve Nissen knows about called CAMELOT which you

can read as saying that a change in blood pressure

of even 5 millimeters of mercury systolic and 3

diastolic might have a reduction of about

33 percent in the kinds of events we are talking

about in people whose diastolic pressure is only

about 100.

That is not definitive. This is a subset

100

of the data and you can look at my slide to see

what I did.

As I said, we don't know as much about the

blood pressure as we should.

So a crucial question is in the larger

assessment of cardiovascular effects; what can we

really study more. My own view is that, given

VIGOR and fairly consistent epidemiologic findings,

it would be difficult to study 50 milligrams of

rofecoxib. I doubt you could write a proper

informed consent.

I take Milton's concern to heart but I

guess my own view is there is probably enough

information about that. But what you could with

respect to other things depends on what you

believe.

Suppose you believe that the

cardiovascular risk of 200, 400, of celecoxib is

not entirely clear. One polyp study says yes and

other studies are not so clear. And you believe,

also, that a class effect is uncertain or, more

particularly, that the effect might not apply to

101

certain doses and certain dose intervals even if

you are inclined to believe that the class does

have a problem.

If you also believe that more needs to be

known about the long-term use of all NSAIDs,

including those that are nominally COX-2-selective

and those that are not, if you believe that new

COX-2-selective agents conceivably could be

developed with appropriate information, and if you

believe the pharmacology gives hypotheses that need

to be tested, not necessarily just believed--sorry

Garret--then here is what you might be able to do.

Again, I am not, in any way, saying who

should do this. This will be a massive

undertaking. But it does seem to me that there is

information we all collectively need as a

community. So I am calling it an ALLHAT study for

anti-inflammatory drugs.

This is just one of what people could

dream up as what might be compared. The drugs, it

seems to me, one might think about putting in it

include ibuprofen, which we think probably ought to

102

be neutral, not bad. It may not have the platelet

effects you want. Naproxen--I am embarrassed to

say this but I am letting myself be affected by the

epidemiology studies. Naproxen sort of looks good.

You might even say it is at least a placebo, but I

am not quite ready to say that.

Diclofenac seems a good model of a regular

NSAID that is really COX-2-selective, at least to a

degree. Celecoxib possibly at more than one dose,

although, maybe for caution, one would want to

think about the lower dose first. Then I have two

other groups that I will be interested in people's

comments on, and I am not totally sure you could

bring these off.

But could one include an aspirin full-dose

study. We know it is an effective agent in

arthritis accompanied by a proton pump inhibitor.

Now, you would have to first show that proton pump

inhibitors really do block the ulcerogenic effects

of aspirin. That is a short-term study and maybe

one could do that. So I will be interested in

whether people think you can bring that off.

The reason for doing it is we know the

effects of aspirin are not unfavorable and we think

they are probably favorable in at least many

103

populations, in populations at high risk and

probably not unfavorable in people at low risk.

The last one that seems worth considering,

and my understanding is that, in many parts of the

world, at least osteoarthritis is treated this way,

to use acetaminophen plus codeine added as needed

and try to do something about the constipation.

That would be as close to a true placebo

group as I think you can get in a setting like

this. So it seems quite interesting.

It is worth saying if one had a new single

agent, my suggestion, and one still thought that

drugs like this should be developed, that the

single agent might be compared to naproxen and I

would still hope for one of the other last two

comparisons as a true placebo.

Obviously, these are all people who need

chronic pain medications. You would want O.A. and

R.A. stratified. I don't believe you could use the

104

APAP group for rheumatoid arthritis but others may

not agree with that. You probably want to study a

range of cardiovascular risks but you probably

would want to study the lower-risk people first.

The reason I say that is anyone with known

coronary-artery disease really has to be given

aspirin just because that is part of treatment and

it isn't clear yet, to me, how aspirin interacts

with the COX-2-selective drugs. You would think it

would make them unselective but the data don't seem

to necessarily say that.

A good question is how big the sample

would have to be and that depends on what you want

to find out. If you are really trying to compare

the drugs with a true placebo, they wouldn't have

to be that large to rule out, say, a two-fold risk

or something like that. We have seen studies with

about 1,000 per group that have distinguished

between drugs. So that is not so huge.

But if you really wanted to get at whether

one drug is a little bit different from another,

you are talking about studies of massive kind. I

105

have asked various numerically qualified people and

the general impression is that if you wanted to

rule out a 20 or 30 percent difference, you are

talking about 50,000 per group. That is beyond my

hopes even for ALLHAT 2.

Obviously, the outcomes of major interest

are cardiovascular death, stroke, AMI and bleeding.

I have heard some thoughts that maybe heart failure

should be looked at in addition but I wouldn't make

that the primary endpoint. I think you can look at

that separately.

A big problem is what to do about blood

pressure. My first thought was that you would

monitor it and treat anything over 120 over 80, but

that really isn't standard practice. So a question

I would raise is whether one could leave people to

go to 130 over 90, would that be acceptable.

A question one could raise is why do this

at all? Do you really need these drugs? We have

heard fairly strong feelings that G.I. intolerance

is not trivial. But my answer is more that we

really don't know enough about the whole range of

106

these drugs. There is no question that people are

going to get something for their arthritis. I am

not entirely comfortable with looking at the data

and saying we know what we need to.

You could sort of deduce that naproxen

usually looks pretty good. It usually beats what

is there except we just heard about a study where

it was a little worse. But it is not clear where

ibuprofen comes. It doesn't show the same thing.

It seems to me there is a serious population need

to find out about these things and to understand

more whether all selectivity is the same.

We have been through diclofenac at length

and it is not clear what one needs. So I think the

idea of doing a large study has weight.

If you believe that it is really all

settled, that cardiovascular risk is clearly

increased with all of the COX-2-selective agents,

ignoring for now which ones are actually selective,

there still are things one might want to know.

It might be of interest to do a study that

still would have the ibuprofen and naproxen groups

107

and might still have my aspirin or APAP groups.

One might consider trying a celecoxib with the

addition of aspirin. I know the results of that

have not shown that any adverse effect seems to be

mitigated, but that still doesn't make much sense

and it might be something one could still want to

test. It would seem that if you added aspirin to a

selective agent, you ought to have a de facto

unselective agent. Of course, that presumes

mechanism and you shouldn't presume mechanism. You

should test it.

Anyway, those are my thoughts. I think my

main point is that there is really a very important

need for better information on the whole array of

these drugs and the kind of study needed to do that

is mind-boggling large. However, people are

already undertaking studies with 25,000 and 30,000

patients already. So it is not as outlandish as I

would have said it was before we started this

process.

Thank you.

DR. WOOD: Okay. I am just interested,

108

why didn't you suggest a PPI with naproxen? For

your ALLHAT study, why didn't you suggest a PPI

with naproxen?

DR. TEMPLE: That is a fair question. I

think the answer on--what did I suggest it with?

DR. WOOD: With aspirin. It doesn't

matter.

DR. TEMPLE: I will tell you the reason.

Full-dose aspirin is just plainly impossible to use

because of massive G.I. intolerance. I believe,

historically based, it is worse than we expect with

naproxen. So I thought you had to do it there

urgently. You could do it with naproxen, too.

That would be okay.

I have to point out that we do not have

definitive labeling or evidence that those drugs

really do prevent this but we have heard about some

studies that suggest it. I do think that is an

early thing to discover.

DR. WOOD: Okay. Understood. Let's move

straight on to Bob O'Neill's presentation who also

is going to do it from his seat.

Issues in Projecting Increased Risk

of Cardiovascular Events to the Exposed Population

DR. O'NEILL: I won't go through the

109

slides. I might point your attention to a few of

them. I will try and do this in five or ten

minutes.

DR. WOOD: Do you want us to have the

slides up, Bob?

DR. O'NEILL: What I was asked to do is

essentially provide a framework. This is a very

difficult problem of projecting risk to the

population. Very little has been published about

how to do this appropriate so I was intending to go

through sort of the logic and the framework of how

you might think about this.

It requires the integration of exposure

data at the national population level and it needs

information relative to how long people are on

drugs and it uses information from the clinical

trials as well as from the epidemiology studies to

the extent that they are relevant to the question

that is being asked.

This is a very difficult problem. It was

not intended to give any estimate, any single

number. It was intended to show how hard it is to

get there and, at the end of the day, how variable

and sensitive the estimate might be to all the

assumptions you have to make.

110

So I used the Vioxx VIGOR and APPROVe

studies as an example of the process that one might

go through. I made the point that event

definitions and many things matter. But I guess if

there is anything that I would like people to take

home is that time matters. The hazard rate

matters. And the hazard ratio matters as a

function of time when you do any of these

projections.

I would just recall two slides. One would

be the VIGOR study which is Slide 12 so that

everybody could remind themselves and Slide 16.

The VIGOR study shows a separation of curves.

Behind that is what is called a hazard rate. I

believe the data supports that the escalation of

the risk increases with duration of exposure.

111

Merck and we have talked about this in the past and

sort of have different views of this, but we seem

to feel that that risk does escalate.

That does not mean that there is no risk

in that picture early on. I think David Graham has

made this point that it may be a power issue but,

nonetheless, it is what it is and I am not

convinced that the epidemiological studies at this

stage add anything to our knowledge about early

risk for the points I made yesterday because I

think time zero matters in terms of looking at the

risk, in terms of how long you are on.

The next slide is Slide 16 which is the

APPROVe study. Similar pattern, only delayed a

year. So instead of the curve separating at

approximately six months, four months, they

separate a little later on. The idea here is that

the relative risks that are summary relative risks

for both of these trials, for VIGOR, for thrombotic

event, it is approximately 2.28 and, for APPROVe,

it is approximately 1.92 for confirmed thrombic

events is an average relative risk averaged over

112

all the time points so that the relative risk at

different times is a function of time.

That is an important concept when, then,

you go and you look at the national projection of

how many people are exposed for how long a period

of time. I won't go through that because they are

in the slides. But we have no data in the United

States to do this. So we did a projection based

upon the IMS National Prescription data, another

separate database that allowed us to look at how

long exposure, success of exposures, might be to

get an idea of how long individuals may stay on the

drug.

Surprisingly enough, a very small

percentage of the millions of people that are

prescribed the drug are on the drug for more than a

year. That is in one of the slides on the

Caremark. So what this meant is you multiply all

these estimates which, essentially, are time. We

calculated a time-specific difference in absolute

incidence rates for the different trials, made a

projection and essentially used in that projection

113

a number of assumptions many of which are not

verifiable, and then came up with some crude

estimate of what might even be an upper bound on a

confidence interval for any estimate.

We probably don't believe it because there

is no real methodology to support that estimate but

nonetheless to say that an estimate is very

variable.

So the bottom line, and the conclusions

here, given the time frame, is that purpose of the

projection effort was essentially just to

provide--this is the last slide; it is Slide 47--it

is essentially to provide a framework for

considering how you would think about developing an

estimate and to provide a range of estimates and,

also, essentially, to point out that there are many

limitations to any estimate that you would provide.

We are not supporting any, or putting

forward any, one estimate but I do believe that we

need to understand this problem by moving away from

summarizing nonproportional hazards in person

years. It is not a good idea. It begs the

114

question as to whether the risk is constant or

whether the risk is dependent on time.

If there is one problem with the

epidemiological literature, it constantly reports

person-year risk as opposed to every one of the

clinical trials we have seen presents a

Kaplan-Meier curve that looks at the time-dependent

risk. Unless you understand that, you can't come

to grips with comparing one drug to another.

You can't come to grips with comparing a

drug to itself. If you look at the VIGOR study

relative to the approved study, they are in

different populations. One is in a population of

R.A. The other is in a polyp prevention trial.

One is at 50 milligrams. The other is at 25

milligrams.

There are many things that need to be

sorted out. So the point here is that this is a

very difficult exercise to project. This was just

a framework to say, here is how you might think

about it. Most of the estimates are fraught with a

lot of danger and have to have many caveats placed

115

on them were you to bank on any one estimate alone.

That is pretty much my bottom line.

DR. WOOD: Bob, just to make sure

everybody in the audience understands what you are

talking about with estimates, what you are talking

about are absolute numbers of people--

DR. O'NEILL: An estimate of the absolute

numbers of individuals that might have been at risk

and had these events if they were exposed--if they

were exposed. This is a model projection.

DR. WOOD: Right. I just wanted to

clarify that. So it is not the relative risk. It

is not the same as what Milt was talking about.

DR. O'NEILL: Right. Exactly. This is a

long discussion to get into the concept of

attributable risk in its own right. Given the

time, I wouldn't be able to do that.

DR. WOOD: So you are talking about the

number of people, these sort of numbers that are

out there.

DR. O'NEILL: Right; to go through that

exercise. It is hard enough to interpret a single

116

study or a collection of studies. To go to an

estimate of what the increased number of events

might be at the exposed level is what this effort

was about, all the different, five different

separate interlinked but disparate databases that

you would need to get there to make this kind of an

estimate.

DR. WOOD: Okay. Good. Thanks.

DR. WOOD: We will take a few minutes, a

very few minutes, for questions to the last two

speakers and then we will take a break and be back.

So the panel needs to remember that they are eating

into their break.

Dr. Nissen?

DR. NISSEN: Quickly, Bob, Bob Temple.

The difficulty, of course, in the ALLHAT study is

that it is very--it seems unlikely that it will get

done. So the question is, putting some constraints

on this, and I thought about this last night in

some detail into the wee hours of the morning, it

seems to me that what we really need for this class

of drugs is a reference standard. That reference

117

standard, unlike many studies, can't be placebo

because you can't treat arthritis patients with

placebo.

So I would submit to you that, if you are

going to do comparisons, that the reference

standard, the best reference standard we have, is

naproxen because we know as much about it as

anything else. We think it is, at worst, neutral

and maybe a little better than neutral.

So I would argue that, if you want to do

ALLHAT light, then what you do is you test every

agent both that stay on the market and that are

proposed to bring onto the market against naproxen

with an adequately sized trial and you set an upper

bound, which we have to talk about, about what the

upper bound of hazard you are willing to accept is,

and the test that you run is on efficacy and on

cardiovascular hazard.

If your drug is beaten by naproxen, you

don't make it. If you can show equivalence within

a reasonable upper bound of naproxen, then we would

be pretty comfortable--I think I would be pretty

118

comfortable that the drug is not going to create a

hazard.

What do you think about that strategy?

DR. TEMPLE: That is actually--I went

through it very fast, but that is actually what I

said at the bottom of one slide. I still would

like to know better whether the naproxen is less

bad or is really good. Therefore, as I said on the

slide, in my heart, I would like to see somebody

try to give full-dose aspirin for a while because

we are really pretty sure that won't be bad.

I think the community, in the long run,

needs that. Who is going to do it? That is a

perfectly good question. I do want to point out,

though, that the way some of the trials were done,

like TARGET, they could have given answers on some

of this, or at least closer. But, because they did

separate trials, instead of randomizing to each of

the treatments, that was obscured.

You could have had a very substantial

naproxen-ibuprofen comparison, but you didn't get

it because of the structure of the trials. So I

119

think it is very important to randomize to each of

the treatments, obviously, whatever it is. But

that would be my best guess at the moment. But, in

line with what Alastair asked before, when you do

naproxen and you are looking at G.I. effects, do

you add a proton pump inhibitor? I think you need

a little more information before you do that, but

you might say that, which then raises the

fundamental question of how much help you get from

being COX-2-selective.

DR. WOOD: Dr. Cryer?

DR. CRYER: I wanted to comment on several

of the questions, Dr. Temple, that you raised as

well to ask a question. I guess I will just ask

the question first. When you say "full-dose

aspirin," are you referring to full

anti-inflammatory doses of aspirin, 3.9 grams a day

or--okay.

DR. TEMPLE: Which I assume most people

will not tolerate and there will be huge bleeding.

So you have got to do something.

DR. CRYER: Right. See, I think that is a

120

non-practical experiment design and I think we have

come a long way from 3.9 grams of aspirin per day,

particularly because of the concerns of the adverse

events, the silicysm, the G.I. events. Clearly,

100 percent of those people are going to have

gastric ulcerations assessed endoscopically.

So I also would prefer one of the newer

NSAIDs, traditional NSAIDs, in that comparison.

With regard to--

DR. TEMPLE: Actually, before you leave

that, do you know what would happen if you added a

proton pump inhibitor to aspirin?

DR. CRYER: Not at 3.9 grams a day. I

don't think anybody thought that would be a

feasible design.

DR. TEMPLE: Short term, then, just to

look at endoscopic ulcers.

DR. CRYER: I don't know and I don't think

that it will ever be known.

DR. TEMPLE: Then I won't get the answer.

DR. CRYER: What I do know is that, if you

give 3.9 grams of aspirin per day in the

121

short-term, greater than 90 percent of your

patients who take aspirin will have endoscopic

ulceration. I don't know what the effect of the

PPI would be.

I wanted to address your last kind of

question that you threw out there of whether or not

a short-term study would show that celecoxib plus

80 milligrams of aspirin would have a favorable

effect, a G.I. effect, compared to a non-selective

NSAID. Those experiments have been done.

With respect to endoscopic ulcer, COX-2

plus aspirin equals traditional NSAID. With regard

to hospitalizations, having said that, there is a

recent study not yet published, epidemiologic study

from Canada, indicating that COX-2 plus aspirin,

hospitalizations for that are less than

hospitalizations for non-selective NSAIDs plus

aspirin. Then we have outcome studies not yet

fully published in the abstract form which indicate

that events on COX-2 plus aspirin are similar to

events on non-selective NSAID plus aspirin--G.I.

events.

DR. TEMPLE: It is possible that if you

add aspirin--I mean, it is sort what I would

expect--is that you would get something that is a

122

lot closer to being--in a cardiovascular sense, a

lot closer to being just a regular NSAID and maybe

you would still have some residual advantage in a

G.I. sense.

But, I must say, the data so far don't

show that. But they didn't seem definitive to me.

It raises the question of--you know, the

idea of COX-2 selectivity is, at least, in part, a

conceptual and promotional idea. As Garret pointed

out the first day, five or six of those old drugs

that aren't coxibs are COX-2-selective. So there

is a whole range. My feeling is we need to

understand the consequences of what all that means

and there is a somewhat artificial separation

between the coxibs and the others because those old

drug at least are partially selective and may have

some of the same properties.

So one of my hopes that we could look at a

range of these.

DR. CRYER: With respect to your last

comment, I am entirely in agreement with that.

DR. WOOD: Let's move on. Dr. Cush?

DR. CUSH: ALLHAT, I like the intention of

it. I would suggest, though, that if you are going

to have a study long enough to pick up some of

123

these events, a year or two, it is going to be

very, very hard to keep O.A. patients on one of

those drugs.

So maybe actually stratifying according to

pure COX-2-specific drugs to COX-2-selective drugs

to the non-selective drugs that are more

predominantly COX-1 and then having a totally

nonsteroidal, non-nonsteroidal group, which would

be the Tylenol group you talked to or other

analgesic agents might work over the long term.

DR. TEMPLE: That would answer a lot of

the questions. My real hope--you have a better

idea whether it is possible than I do--is that you

could actually find a population that could be

given what we are pretty sure is a

cardiovascular-neutral treatment. That is really

124

the only way to pin this down and it does seem

worth pinning down.

DR. WOOD: Dr. Hennekens?

DR. HENNEKENS: I think I gleaned from Dr.

O'Neill that if we determine there is a class

effect that it varies not just by drug and dose but

by duration of therapy. From Dr. Temple, the

comment that--I am very attracted to the concept of

what I would call a large simple trial rather than

an ALLHAT trial. I think there is merit in seeing

aspirin studied in therapeutic doses and I think

there is evidence that anti-inflammatory effects

are seen a doses far lower than the 3.9 grams.

But the question I have for Bob is there

are three currently marketed FDA-approved coxibs.

So would you include valdecoxib and 25 milligrams

of rofecoxib in your design?

DR. TEMPLE: Part of the reason I didn't

address that is I figured that is what the

committee is going to talk about. I was willing to

say that the celecoxib data look funny enough so

that you might consider it.

DR. WOOD: That is part of what we are

going to discuss.

DR. TEMPLE: That is what you are going to

125

discuss so I didn't address it.

DR. WOOD: Let's move that to later. Dr.

Domanski?

DR. DOMANSKI: I will pass.

DR. WOOD: Dr. Abramson?

DR. ABRAMSON: Thank you. I want to

probably say something rather naive in support of

the study, Bob, and that is that we are at a moment

where we can do a paradigm shift, meaning that

study that you propose is an important one but it

is very large and it is going to be very hard to

get any resources to do that.

I think we are at a moment where for the

companies and the FDA and the government to think

about a collaborative study where, if you have a

drug that has some--this information is important,

that we put together a collaboration among industry

to do a multi-arm study of multiple drugs. It is

something, you know, in the osteoarthritis field,

126

the companies have supported largely this

osteoarthritis initiative through the NIH to look

at outcomes in large numbers of patients.

I think what we need is a similar COX-2

initiative where either with the FDA or the NIH

participating, with collaboration among industry,

we are doing a multi-armed large study with

biomarkers, with pharmacogenomics studies, with

genetics and other blood pressure, but try and do

it in a utopian way.

I think everyone here wants to get the

right answer, whether it is in industry or here at

the table. This could be a good opportunity to do

something very differently than we have done before

in a large trial.

DR. TEMPLE: I don't disagree at all. I

mean, some of the drugs are generic. They don't

have any company that is massively interested in

them. So it is going to be a mixture of

government, generosity and a wide variety of other

things that are scarce. So I don't know how

to--you noticed I didn't have a slide on how to do

127

this.

DR. WOOD: Dr. Ilowite?

DR. ILOWITE: Just a minor point. I

understand the need for a cardiovascular-neutral

anti-inflammatory drug in an ALLHAT study. But I

was a little confused because I am aware of some

literature directed at people who are interested in

Kawasaki disease suggesting that high-dose

anti-inflammatory aspirin is actually prothrombotic

because of differential effects on prostacycline

and thrombotics.

DR. TEMPLE: There are aspirin studies

going back to at least moderate doses that show

beneficial effects. It is not just 80 milligrams.

It is certainly at least a gram a day. Some of the

early ones were more than that. That is worth

thinking about. I am encouraged by the thought

that you might be able to get away with doses less

than 3 grams. So I didn't know that it was

considered prothrombotic. I thought aspirin always

looked good. But that is not up to grams. I don't

think any of the studies have done anything like

128

that.

DR. WOOD: We will give Dr. Fleming the

last word.

DR. FLEMING: I am just debating whether

to do it now or after the break.

DR. WOOD: Let me help you. Go ahead.

DR. FLEMING: Now?

DR. WOOD: After the break will be great.

DR. FLEMING: All right. I will wait.

DR. WOOD: We will take a break and then

we will be back here in ten minutes.

(Break.)

DR. WOOD: Okay, folks. Let's get

started. The next presentation will be given by

Sharon Hertz who is Deputy Director of the

Division.

DR. HERTZ: Thank you. I am just going to

spend a very few minutes summarizing some of our--

DR. WOOD: Let me, in fact, just before

Sharon begins--Sharon Hertz has passed out a

handout that includes a lot of her slides. In the

interest of time, she has graciously agreed to

129

delete some of these slides and just focus on a

smaller subset of what is in the handout.

However, the committee does have the

handout and the committee may find that handout

useful for referring to some of the data.

DR. HENNEKENS: Alastair, a quick comment.

I want to make a quick clarification on the earlier

comment about pro-inflammatory effects of high

doses of aspirin.

DR. WOOD: Sorry; I missed that. About

what?

DR. HENNEKENS: In the randomized trials,

135 randomized trials with over 212,000 randomized

subjects, whether the doses of aspirin are 75

milligrams or up to 2 grams a day, there are

significant cardiovascular benefits to aspirin even

at high doses. The issue, as Bob pointed out, at

the high doses, is not that there is a reversal of

the benefit but that the side effects are

increased.

So I think that is an important point to

make.

DR. ILOWITE: I just wanted to say that in

pediatrics, we think of anti-inflammatory doses as

100 milligrams per kilogram. So those are the

130

doses I was speaking of.

DR. GIBOFSKY: Finally, the high-dose

aspirin that would be necessary to treat patients

with rheumatoid arthritis of 3.9 grams or greater

would have significant problems on the stomach, as

Dr. Cryer said, significant problems on the hearing

of the patient and significant problems, perhaps,

on other organ systems as well. It is not a study

that could be easily undertaken.

DR. HENNEKENS: I won't debate the value

of the study of 3.9 grams of aspirin but, from the

perspective of anti-inflammatory effects, they have

been observed at doses of 2 grams of aspirin a day

and, in fact, there are randomized studies going on

directly comparing that somewhat higher doses of

maybe 1 to 1-and-a-half grams a day might have

significant anti-inflammatory as well as

anti-atherogenic effects as measured by endothelial

function, nitric oxide formation and other

131

parameters.

So I don't think that the traditionally

high doses are the ones that necessarily would need

to be done. But I don't want to debate whether we

should be studying doses of 4 grams of aspirin.

DR. WOOD: What you are telling us,

Charlie, is that you are comfortable that there is

an antithrombotic effect at the high doses of

aspirin. Is that right? Okay. Good.

Dr. Cush wants to say something.

DR. CUSH: Again, you need not

anti-inflammatory doses but analgesic doses which

can be substantially lower. I do want to make a

statement with regard to a study that wasn't

presented here that I think is germane and we

should know about it, and this is quick. There is

a very large trial that is NIH supported that is

called the GATE study, glucosamine in

osteoarthritis of the knee.

This is a 1588 study that is completed and

is currently being analyzed. That Data Safety

Monitoring Board of the study has analyzed it for

132

cardiovascular risk because there is a Celebrex

arm. There are five arms in this 1500-patient

study; placebo, Celebrex 200 milligrams once a day,

glucosamine only, chondroitin sulfate only, and

glucosamine and chondroitin sulfate.

The outcome here, in a six-month trial, is

pain reduction in osteoarthritis in the knee.

Because of all this press and what not, they have

looked at the safety outcomes and they have not

shown any increase in cardiovascular events

including M.I., any difference between the Celebrex

group and the other four control groups.

DR. WOOD: Let's move on to the program.

Dr. Hertz?

Summary of Meeting Presentations

DR. HERTZ: There are now several versions

of my slides around and you are free to look at

whichever interests you. There is one correction

on the lumeracoxib slides from the original set

where I substituted the word diclofenac for

ibuprofen. So those of you looking at those slides

just be aware of that, please.

What I am really just going to do now is

just focus down again some of the reasons why we

are here. This would not be the current slide set.

133

Any help here?

Looking at the most recent set that were

handed out, and we will just work from there

because there is not a lot of data anymore to

present, but, basically, I want to just point out

that we are here because we do recognize that pain

drugs are critically important, that the

COX-2-selective NSAIDs have been extensively

studied and there are, over time, studies that

revealed new potential uses as well as new risks.

We need to determine how we feel about

these risks. Are they limited to individual

products? Are they applicable across the group of

COX-2 selectives and how far does this extend to

the nonselective anti-inflammatories.

There is a slide that describes--

DR. WOOD: Sharon, apparently everybody

has hard copies of your slides.

DR. HERTZ: Right.

DR. WOOD: So if you want to just go

through them and refer to the slide number, that

would probably be helpful to people.

DR. HERTZ: Okay. If we go to the third

slide, you can get a sense of the sizes of the

databases that were presented in the individual

134

reviewer descriptions of FDA reviews.

A couple of points. The numbers there

reflect predominantly patients on the drug of

interest as opposed to the entire database. The

outcome studies are more reflective of the entire

populations including comparators. These drugs

were assessed and have been assessed over time in

fairly large numbers of patients.

I think it is useful to note that we have

not approved, in this country, all of the

COX-2-selective NSAIDs that have come to us in

applications for a variety of reasons. Some of

these may be related to cardiovascular-risk

assessment. Some may be related to

non-cardiovascular-risk assessment which we really

haven't gotten into in this setting.

In addition, you may also note that

parecoxib has not yet been approved in this country

although it has been approved elsewhere. So I

think that we have a lot of issues to consider with

these products.

When we reviewed the studies that have

been presented, we see that there is some increased

risk for cardiovascular events but one of the key

issues here is that the results are not consistent

135

across studies and across situations. We also have

seen that there is risk that is being associated

with some of the nonselective products.

So we have a story of conflicting data. I

am up the Slide 5. We have data that has been

present across short- and long-term studies, the

epidemiologic studies. The challenge is to compare

across populations, across comparators. It is

striking that sometimes very similar study designs

have very different results.

It is possible there is more than one

mechanism. Again, the data has been inconsistent

with the NSAIDs. We also have conflicting

136

information coming back on what occurs in the

context of concurrent aspirin use. It is really

unclear if aspirin use has a truly meaningful

effect on whether there is any G.I. benefit of the

COX-2-selective products. That has not been clear

either.

I have been asked to point out that, in

addition, time to onset of risk is something that

we need to consider very importantly, too, which,

again, is something that is evident when we look at

the study data and important in our deliberations

for this.

So, in spite of this conflicting data and

the many questions, we have to move forward. We

have to determine what the role of approved

products are on the market today, what additional

studies are necessary, what studies would be most

helpful.

I am going to summarize and combine some

of the questions that we have posed. These are

questions we dearly would like input from the

committee. To start, if we think about the first

137

three questions, does the available data support a

conclusion that celecoxib, rofecoxib and valdecoxib

significantly increase the risk of cardiovascular

events. Does the overall risk-versus-benefit

profile for each of these support marketing in the

U.S. If yes, in whom? And which of the potential

benefits of celecoxib or the others outweigh the

potential risks and what actions would you

recommend that we consider implementing to ensure

safe use?

I think it is also important to understand

that some of these answers are going to depend on

if we think that this is a fairly uniform class

effect and, if not, we are going to have weigh the

amount of information available for each of the

products. It is not the same. We don't have the

longer outcome studies, for instance, with

valdecoxib at this point.

Question 4 asks if the available data

support a conclusion that one or more of the

COX-2-selective agents increase the risk of

cardiovascular events and what is the role of

138

concomitant aspirin in attempting to mitigate that

risk. What additional clinical trials or

observational studies, if any, would you recommend

as essential for us to further evaluate celecoxib,

rofecoxib and valdecoxib?

What about to further evaluate the

potential G.I. benefits for these same products?

Would you recommend that the labeling for these

products include information regarding the absence

of long-term controlled clinical-trial data

assessing potential cardiovascular effects and if

you have a recommendation for how that should be

conveyed in terms of warnings, boxes and such.

What additional trials would be essential

to evaluate the nonselective nonsteroidal

anti-inflammatory drugs particularly with respect

to cardiovascular risk? Similarly, what will now

become essential for products under development

prior to approval to help gain approval?

We have to determine what studies would be

necessary to evaluate the cardiovascular risk of

these products and how much information do we need

139

to know about the gastrointestinal risk? If

preapproval studies recommended as essential do not

demonstrate an increased risk for a cardiovascular

event, how would you propose the FDA handle that

information in the labeling? Would the absence of

a cardiovascular-risk signal preclude the need for

any warnings or precautions in the labeling of a

new product or should we rely more on a class

warning or precaution in the absence of a signal of

increased risk in the preapproval databases?

If you think a class warning is

appropriate, please advise with particular

attention to whether you recommend it apply to all

NSAIDs or only COX-2-selective NSAIDs.

So I want to thank everybody here for

their time and their commitment to helping us

through this extremely challenging program and we

really look forward to hearing your deliberations

and your recommendations.

Thank you.

DR. WOOD: Thank you very much.

The companies have also asked for two

140

minutes to respond. We all heard the rules

yesterday so it is two minutes. Microphone gets

turned off two minutes later and just keep moving.

Sponsor Responses

DR. HARRIGAN: Could I have Slide No. 1.

This is Harrigan from Pfizer. What I would like to

do is first to summarize what we know about

celecoxib and what we think that tells us about the

benefit:risk equation for that drug.

I make the point in this slide about

Celebrex being extensively studies and to remind

the committee of the contrast of the very widely

used nonspecific NSAIDs. On the next point, we see

that efficacy has been demonstrated in arthritis

pain and familial adenomatous polyposis. Our

prescription data and observational study data tell

us that approximately three-quarters of patients

who are taking celecoxib are receiving daily doses

of 200 milligrams or less.

Celebrex does have a favorable G.I. safety

profile, a point emphasized by the very relevant

G.I. safety findings that we heard about this

141

morning from ADAPT compared to over-the-counter

doses of naproxen.

Cardiovascular risk was not detected in

the setting of treating arthritis patients

understanding all the caveats about that data that

we have heard over the past two days. In APC, an

increase in cardiovascular risk was reported

apparently in a dose-related pattern. In contrast,

two additional long-term placebo-controlled trials

did not find evidence of increased cardiovascular

risk at daily doses of 400 milligrams.

The comment about the ADAPT findings is

supported by the initial announcements from

National Institute of Aging. We await that data

with great interest, particularly given the size,

the duration in the elderly population study which

would lead us to believe, expect, that the number

of events in that trial will exceed the number of

events in either or both of the other two trials

combined.

The final ADAPT data and the polyp

efficacy data will make significant contributions