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 II

Thursday, February 17, 2005

8:00 a.m.

Hilton Gaithersburg

620 Perry Parkway

Gaithersburg, Maryland

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

Alastair J.J. Wood, M.D., Chair

Kimberly Littleton Topper, M.D. Executive Secretary

ARTHRITIS ADVISORY COMMITTEE MEMBERS

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

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

MEMBERS

Peter A. Gross, M.D., Chair

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 Rep.

Louis A. Morris, Ph.D.

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

Robyn S. Shapiro, J.D.

Annette Stemhagen, Dr.PH., Industry Rep.

FDA CONSULTANTS (VOTING)

Steven Abramson, M.D.

Ralph B. D'Agostino, Ph.D.

Robert H. Dworkin, Ph.D.

Janet Elashoff, Ph.D.

John T. Farrar, M.D.

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

Thomas Fleming, Ph.D.

Charles H. Hennekens, M.D.

Steven Nissen, M.D.

Emil Paganini, M.D., FACP, FRCP

Steven L. Shafer, M.D.

Alastair J.J. Wood, M.D. (Meeting Chair)

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

FDA CONSULTANTS (NON-VOTING)

Byron Cryer, M.D. (Speaker and Discussant)

Milton Packer, M.D. (Speaker only)

NIH PARTICIPANTS (VOTING)

Richard O. Cannon, III, M.D.

Michael J. Domanski, M.D.

Lawrence Friedman, M.D.

GUEST SPEAKERS (Non-Voting)

Garret A. FitzGerald, M.D.

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

Bernard Levin, M.D.

Constantine Lyketsos, M.S., M.H.S.

FDA (CDER)

Jonca Bull, M.D.

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

Brian Harvey, M.D.

Sharon Hertz, M.D.

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

Sandy Kweder, M.D.

Robert O'Neil, 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.

Steven Galson, M.D.

Kimberly Littleton Topper, M.S., Executive

Secretary

C O N T E N T S

Call to Order:

Alastair J.J. Wood, M.D., Chair 5

Conflict of Interest Statement:

Kimberly Littleton Topper, M.S. 5

Interpretation of Observational Studies

of Cardiovascular Risk of Non-steroidal Drugs

Richard Platt, M.D., M.S. 8

Review of Epidemiologic Studies on

Cardiovascular Risk with Selected NSAIDs

David Graham, M.D., M.P.H. 37

Committee Questions to Speakers 89

Arcoxia (etoricoxib)

Merck Research Laboratories

Sponsor Presentation

Sean P. Curtis, M.D. 152

FDA Presentation

Joel Schiffenbauer, M.D. 189

Lumiracoxib

Novartis Pharmaceuticals

Sponsor Presentation

Introduction

Mathias Hukkelhoven, Ph.D. 201

Gastrointestinal and Cardiovascular Safety

of Lumiracoxib, Ibuprofen, and Naproxen

Patrice Matchaba, M.D. 205

Open Public Hearing 236

FDA Presentation (Lumiracoxib)

Lourdes Villalba, M.D. 336

Committee Questions to Speakers 346

Committee Discussion 410

P R O C E E D I N G S

Call to Order

DR. WOOD: Let's get started and welcome

back to another day. We are going to begin as on

the agenda seeing we worked late last night.

A couple of housekeeping things first. As

they say in the movie theater, please turn off your

cell phones. We don't have the one that sort of,

you know, spars you into space if you do that, the

ejector seat, but then please don't answer your

calls in here, so we don't have to hear the

beginning of your conversation.

Kimberly, are you going to read the

conflict of interest? Okay. Go ahead.

Conflict of Interest Statement

MS. TOPPER: The following announcement

addresses the issue of conflict of interest with

respect to this meeting and is made as 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 involved

many industrial sponsors and 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 any of the 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 of 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 potential conflicts

of interest, but because of the general nature of

the discussions before the committee, these

potential conflicts are mitigated.

With respect to FDA's invited industry

representative, we would like to disclose that Dr.

Annette Stemhagen is participating in this meeting

as a non-voting industry representative acting 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 Development Services for

Covance Periapproval Services, Inc.

In the event that the discussions involve

any other products of firm not already on the

agenda for which FDA participants have a financial

interest, the participants involved 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 first whose products they may wish to comment

upon.

Thank you.

DR. WOOD: Thank you.

Let's go right to the first speaker, Dr.

Platt, who is going to tell us about observational

studies.

Interpretation of Observational Studies of

Cardiovascular Risk of Nonsteroidal Drugs

Richard Platt, M.D., M.S.

DR. PLATT: Thanks. The framers of the

meeting thought it would be useful at this point to

have a discussion about observational studies to

put us all on the same page.

There was a view by some that the

expertise around the table might be uneven and it

would be worthwhile to have some discussion about

some of the basics. It is clear that that is not

the case.

I realize that a number of the people here

have written a book and several of my teachers are

here, so to that extent, I think we can either make

this a quick discuss or use this as an opportunity

for a real interactive discussion, because there

are some hard questions here and no matter how we

sort we out, we are going to be left with less than

in the way of firm answers than we would like.

I also understand that there is a point of

view that says that there are lies, damn lies, and

observational studies, so part of what I think is

worth doing is using this time maybe to take our

temperature about whether and under what

circumstances we can put weight on observational

studies.

We saw a version of this slide last night

actually in the last presentation about why perform

observational studies at all, because I subscribe

to the general view that all things being equal, a

clinical trial, a randomized trial is more

credible, provides more information than an

observational study.

The problem is all things aren't always

equal and so there are reasons to ask what we can

learn from observational studies.

I think the most important of them is no

matter how well a clinical trial is designed, the

individuals who are recruited and consented to a

clinical trial are inherently going to be different

from the actual population of users, and if we want

to understand how an agent performs among real

users in the way they actually use the drug, then,

I think there is no escape but to look to

observational studies.

Additionally, observational data is by

definition there, so when a pressing question

arises, sometimes observational data is the first

way we can get insight into the relationship

between the drugs we care about and the exposures.

I think in that regard, these studies can

often be thought of as helping us identify the

areas in which it would be most fruitful to invest

in full-blown randomized trials. We will never

live in a world where we are able to do all the

randomized trials we care about.

I know that Charlie Hennekens' landmark

randomized trial of aspirin was preceded by, as I

recollect Charlie, a large number of observational

trials, it made you think that it was reasonable to

do those randomized trials, so observational

studies can be useful in that regard.

Finally, when we are talking about trying

to understand effects that are relatively unusual,

we stress even the largest clinical trials. We

talked yesterday about the fact that the most

recent drug approvals have used much larger

populations in the NDA phase than had been studied

in the old days, and yet they are still small

compared to the numbers needed to parse out

relatively small differences.

There are a lot of different kinds of

observational trials. I have listed a few of the

most common. The ones between the lines here are

the ones that are really the subject for discussion

here.

Tom Fleming made the absolutely correct

and somewhat counterintuitive point that it is

often more difficult to do good observational

studies of relatively common outcomes than rare

ones, and because of that, the group of studies

that I think at least are reasonable to consider

for looking at relatively common outcomes are

case-control studies, nested case-control studies

and cohort studies.

We have examples of each in the materials

that have been handed to us. The study by Kimmel

is a pretty traditional case-control study. The

studies by Ray are cohort studies, as is the Aramis

study. The study by Dave Graham, the Solomon study

are nested case-control studies.

Just as a quick reminder, the

distinguishing feature of cohort studies is the

fact that the study population is defined on the

basis of whether people are exposed to the drug or

not, and then we look forward to what happens to

them. In that way, they are exactly comparable to

clinical trials, with the big difference that the

assignment to drug is not randomized.

The strengths of those compared to

case-control studies are you have a reasonable shot

at the outset of selecting individuals who are

representative of the group that you are trying to

study, and if you organize the study properly, you

have a reasonably good chance of getting unbiased

exposure assessments.

The weaknesses, particularly of

observational cohort studies is that just because

individuals had the right drug exposure at the

outset, they may change that. You can deal with

that with an intention-to-treat design, but you pay

for a price for that, and in observational studies,

loss to followup is a big problems.

We are particularly plagued by that

because the large majority of the observational

studies we are working in are ones that use

administrative data from one sort of health plan or

another, and individuals move in and out of health

plans, so that it becomes difficult to follow them

over time.

Case-control studies, remember are ones

that start with individuals who have the outcome we

care about, myocardial infarction or myocardial

infarction and sudden death, and compares them to

individuals who haven't had that experience, then,

you look back and ask what their drug exposures

are, the reasons for doing those studies are that

they are, first of all, very efficient studies.

You don't have to study thousands and

thousands. You can study as many cases as you find

and a reasonable number of controls, and you can

look back and classify exposure however is most

useful, and that is a very convenient and versatile

feature of case-control studies.

The big weaknesses are that it is very

hard to assure oneself that the cases and the

controls are really representative of the

populations that you care about, and for

conventional case-control studies, for instance,

the study by Kimmel that we are going to look at,

it takes a lot of work to be sure that people who

know what they have already experienced an MI don't

differentially report their exposure to the drugs

that we care about.

That can be for all sorts of reasons and

it might not even be wrong, but the individual who

has had an MI and might be just thinking harder

about whether he or she had been exposed to a drug

that we care about.

By the way, nested case-control studies,

for instance, the study that David Graham did is a

hybrid that really, in my view, draws many of the

strengths from both designs, that is, because

nested means the case-control study is nested in a

defined population, so it has a lot of the

strengths of cohort studies and some of the

efficiencies of the case-control studies.

The differences between the observational

studies and randomized studies are pretty clear.

Randomized trials have the tremendous advantage

that there is lots more reason to expect the

treated and untreated groups to be comparable to

one another.

There is a lot more opportunity to be sure

that the outcome assessment and adherence to

treatment are good or at least well known, and we

have reviewed the difference for the observational

studies.

I think it is worth making the point that

there are a substantial number of similarities

between observational and randomized studies. Just

because we randomize individuals in randomized

studies, it doesn't mean that the treated and

untreated groups are comparable.

We talked about a study yesterday that was

a randomized trial where there was a substantial

imbalance in important risk factors. So, it is

incumbent no matter what kind of study you do, I

think to look for comparability, and both studies

have as potential weaknesses that there are risks

of false positive results and doing subgroup

analyses and multiple comparisons increases that

risk.

We talked a fair amount about that

yesterday, and both are at risk for false negative

results. That can be partly because the studies

may not be powered well enough either because there

is insufficient sample size or individuals aren't

studied for a long enough duration to see the

biological effects that we care about, or a

vulnerable group just isn't included.

That is a problem with both kinds of

studies and I think all studies have to be

evaluated on their own merits, so let's just step

through the various places where observational

studies might be into trouble or at least the

things that need careful assessment when we look at

these studies.

The first is are we studying the right

outcomes. It is essentially impossible in any of

these observational studies to use the kind of

rigorous adjudication that is a hallmark of the

randomized study, so I think we are going to have

to ask ourselves are these outcomes good enough.

The several kinds of outcomes in the

studies that we have been asked to look at are

hospitalized MIs. The case-control study by Kimmel

uses survivors. It had to use survivors because

they were collecting the exposure information by

interview after the individuals had left the

hospital, so if we care about all MIs, then, that

study isn't going to tell us what we want to know.

Some of the studies use MI and

out-of-hospital sudden death by linking to vital

statistics records. I think that is probably the

closest we can get in observational studies to the

intention-to-treat all outcome designs of the

randomized trials, and some of the studies use

composite designs.

You have to ask are these outcomes

measured appropriately. Most of the studies that

we are looking at use some form of automated

medical record or claims data that have been, in my

view, reasonably well validated. That is, there is

a moderate literature showing that claims data are

not so bad for studying acute myocardial

infarction. They have sensitivities in the 90s and

positive predictive values in the 90s.

So, they are not perfect and I think we

will have to ask as we review the studied can the

amount of uncertainty that we know exists in those

account for the effects that we see, or could they

obliterate effects that we would like to see and

which aren't there.

My sense is that that is probably not a

sufficient explanation to dismiss the studies that

we are looking at. The issue of bias is one that I

think always has to live as a sub-text, but quite

frankly, in the studies that do outcomes in the way

we have been describing, I don't think that is a

serious problem.

For cohort studies, we have to ask are we

studying the right population, and here I think we

really do have to stop and ask carefully. One is

are these people selected from the population under

study. I think in most of these examples, they are

reasonably representative, that is, a study of the

people of Ontario or members of a large health

plan.

I think that the data systems that are

used to identify the individuals in the cohort are

good enough to give us reasonable belief that we

are identifying either all the people or a

representative sample of them.

I think there is a fair question of

whether they are representative of the larger

population. We could ask are health plan members

systematically different from the general

population of individuals who are taking these

medications.

The range of studies we have include

health plan members. I think that there is

reasonable information that they probably are

representative, at least with respect to the drug

myocardial infarction outcomes that are studied.

Studies in Medicare and population-based studies,

such as those in Canada, I think also give us

reason to think that they are representative.

But there is an important consideration

about whether there are issues about the way

clinicians practice in those setting that might

have a serious impact on selecting individuals. In

particular, to the extent that formularies are

restrictive of, say, newer or more expensive drugs

like the COX-2 inhibitors, but I think we have to

ask very carefully whether the factors that would

influence the prescribing of one class of drugs

over another is likely to seriously impact the risk

of these outcomes.

Additionally, if there are cost

differentials for these drugs, it may be that there

is some form of self-selection that causes

individuals who are sicker to receive these drugs,

and I think that it is incumbent on us to expect

that to be a problem in every one of these

observational studies and to ask how well do these

studies do in adjusting for that. I will circle

back to that in a moment.

I think we have to be concerned about

whether we are studying people who have had prior

NSAID exposure, in which case we would be worried

about survivor biases, of finding the individuals

who are relatively immune to these problems.

Finally, there are study design issues

about whether there are restrictions of eligibility

that might importantly color the data. For

instance, at least one of the studies we are

looking at requires individuals to have received at

least two dispensings of a nonsteroidal agent in

order to be eligible.

That means that you have to live long

enough to have two dispensings, so it certainly

doesn't tell us anything about the early effects of

these drugs, and it might in an important way color

the results with regard to later exposure.

There is an important question which is

not unique to the observational studies, which is

who are the right comparators. We had a number of

discussions about that yesterday. I think that all

the issues that we discuss with regard to the

clinical trials are applicable here. In

particular, there is a lot of reason to want to

compare to other nonsteroidal users because that

gives the best chance of having a group that is

similar with regard to underlying disease status

and presumably risk of myocardial infarction.

Similarly, it is possible to say that if

you really care about COX-2 selective agents, you

should compared one COX-2 selective agent to

another.

That leaves us in the uncomfortable

situation of not knowing what is the risk compared

to no use at all, so we have some comparisons that

do look at non-users or at least remote users, and

that has its strengths. It has the big weakness,

of course, of putting us at risk of making

comparisons against groups that are unrelated.

So, we are really talking here of mostly

about a study like the Kimmel study, not the nested

case-control study. The other kinds of concerns

that raise red flags are the real concern about

losing cases who make the group who are studied

unrepresentative.

I would point out to you, for instance,

that in the Kimmel study, only half of the MI

survivors who were identified were actually

interviewed and therefore part of the formal

analysis.

We already talked about the fact that

since that study was limited to MI survivors, that

restricts us to a less serious set of outcomes.

The other problem that really bedevils

conventional case-control studies is knowing

whether the group of people who are selected as

comparators are really comparable.

I think that is one of the reasons that

there is so much interest in doing nested case

control studies, because at the end of the day it

is really extremely difficult to satisfy oneself

that controls really are appropriate.

Much of what we need to be concerned about

in these studies is understanding exposures. Part

of the issue is understanding how to characterize

exposure. This is both a strength and a weakness

of these studied.

You will remember I made the point at the

outset that if we want to understand how drugs work

in actual practice, that we have to do

observational studies. On the other hand, that

means we have to find a reasonable way to

characterize these drugs.

We talked yesterday I think about all the

important issues of understanding whether we had to

look at absolute dose or cumulative effects or

whether the effects start early or whether they

start late.

I think that the best of the studies that

we are looking at tackle a number of these issues.

I will mention in a minute some of the ways that

these studies have gone about that.

I think in terms of ascertaining exposure,

it is probably reasonable to put the most reliance

on the studies that use administrative databases of

pharmacy dispensing, but I will just make the point

that we have to be clear that these studies are

done in situations where we have reason to expect

that the administrative databases are correct.

I think all the studies we are reviewing

are ones where the investigators were careful to

know that the individuals really had a drug benefit

that was operating at the moment, that would likely

find the prescription drug exposures that we care

about, but as a general proposition, you can't

assume that that is the case.

Most health plans have some kind of

restrictions on benefits that might lead

individuals to change their benefit status, so

there would be periods of time when we might know

that they had an MI, and we might not know that

their drug exposure is at the moment.

I will return to a point that we touched

on yesterday, which is that although almost all of

the studies that we are talking about report their

results as relative risks, a 2-fold increase in

risk, a 70 percent decrease in risk. What we

really care about is the absolute difference in

risk.

So, that is not different between

observational studies and randomized studies, but I

think it is really a critical piece of our thinking

about the problem that we are dealing with.

The second thing that is just worth

recalling is that when we talk about a 95 percent

confidence interval, that our expectation about

where the true value lies is not uniformly

distributed over that interval.

Our best guess about where the true value

lies is around the point estimate, and if that

point estimate is wrong, the large majority of the

uncertainly is pretty close to that point estimate,

so that it is particularly not helpful, in my view,

to pay enormous attention to p values.

The difference between a p value of 0.05,

as shown here, and a p value of 0.01 and a p value

of 0.13 is not all that enormous in terms of the

biological impact.

I think one of the things that is a

particular concern that we need to pay attention to

in these studies is the fact that it is easy to

look at a lot of different comparisons, and to the

extent that we do that, we are going to have to

just be careful to know that the strength of any

one comparison is weaker than it appears to be.

For instance, this is a quote from one of

the studies that we are looking at. We undertook

an observational study examining the association

between rofecoxib, celecoxib, other nonsteroidals

and myocardial infarction.

Well, there is no primary hypothesis

there, and the results for all of the

nonsteroidals. They are all interesting to look

at, they are all associated with p values. Those p

values are all relatively too extreme given the

fact that there are so many comparisons.

It is a problem for randomized trials. We

talked about subgroup analyses. It is important to

do those studies, those subgroup analyses, but

absent having specified a principal hypothesis at

the outset, I think that we have difficulties in

knowing how much weight to put on any particular

one.

We talked a lot about confounding. That

is one of the most important concerns in randomized

trials. I know you all know what confounding is.

It wasn't obvious to me when I was making these

slides that everyone knew that, but the example, so

that we have it in mind is if what we know is drug

A versus drug B, and MI or no MI, and we don't take

into account important confounders, we can get

importantly incorrect results.

So, here is an example of an aggregate

analysis with a relative risk of 1.5 among 2,000

people who are exposed to two drugs. If you break

it apart and see that in the high-risk group, drug

A accounted for 80 percent of the exposure, and in

the low-risk group, drug B accounted for 80 percent

of the exposure, you see that in each of those two

categories, the high-risk group and the low-risk

group, that, in fact, there is no association

between drug and outcome, but you have to take them

apart to do that.

Well, the good news is if you know what

the confounders are, and you have measured them

accurately, it is possible to adjust for them, and

all of the studies we are looking at do a pretty

job of adjusting for the confounders that we know

about, so I guess one of the questions is how well

do they do at identifying the important

confounders.

I would say not bad on a lot of that.

That is, if you take, for example, the Graham study

or the studies that Wayne Ray did in Tennessee

Medicaid, there are a number of strengths. I will

sort of stop and back up on the things that make

these look like relatively more credible studies in

the scheme of the factors that we care about.

They are inception cohorts of nonsteroidal

users, that is, they are individuals who had to

have been members of the health plan for at least a

year before they received their nonsteroidal.

There was a lot of information about their

underlying medical status that was available to the

investigators using both claims data and medical

record data to ascertain cardiovascular disease

along a number of dimensions, utilization of

procedures like surgery or angioplasty or

diagnostic procedures that are intended to find

cardiovascular disease, hospitalizations, emergency

room visits, and a substantial amount of

information about the medications that these

individuals took that was related to or plausibly

related to cardiovascular risk factors.

Those large number of factors were used to

create separate risk models using only the

unexposed, and then to use those risk models to

create risk indexes for the individuals to use as

an adjuster for underlying cardiovascular risk.

Is it perfect? No. Is it pretty good?

It seems to me that it meets the sniff test of

saying that it has a reasonable chance of

identifying important confounding.

Unfortunately, there are a number of

important confounders for which health care systems

typically don't have good data, like smoking, OTC

NSAID use, obesity, family history, and those are

typically much more problematic.

Some of these studies have worked pretty

hard to try to either deal with it or understand

whether it could be an important problem. One of

the handouts we had, for instance, was the study by

Schneeweiss and colleagues who looked back at one

of the studies by Solomon that was performed in the

Medicare data set, and asked how important could

these unmeasured confounders be.

They actually had access to information

from the Medicare Beneficiary Survey that asked

representative Medicare beneficiaries detailed

questions about many of the things that we would

are about. They weren't the people who were

involved in that case-control study, but if you

assume that the beneficiary survey, members were

representative and they gave plausible answers, it

is possible to extrapolate back to the source

population, and the take-home message from that

work, the answer didn't change very much, which is

really what we want to know, not sort of the

absolute difference, but whether those unmeasured

confounders are important enough that they could

cause a difference.

I think we still have to be concerned at

the end of the day, we still have to be concerned

about residual confounding as a potentially

important problem.

One way I think that we can draw relative

assurance from that work of adjusting for

confounding is to ask how much did the estimate of

risk change between the unadjusted and the adjusted

result.

I think there is a world of difference

between an unadjusted result of 10 and an adjusted

result of 1.5, and having an unadjusted result of

1.6 and an adjusted result of 1.5. The former, I

think the reasonable assumption is we arguably

haven't been able to deal with confounding in a way

that would let us believe that 1.5 means something.

I think there is a much stronger case to

be made when adjusting for important confounders

that we know about doesn't change the risk estimate

very much, that that is a relative more credible

answer.

Having said that, I think that

observational studies are best at finding relative

risks that are more than 2. I think that I would

pay some attention to relative risks of 1.5. I get

very nervous about adjusted relative risks of 1.2.

That doesn't mean that they are not right

and I don't ignore them, but if we ask is that for

sure the answer, my response to that is I am just

less certain about that.

I think we are always left at the end,

while we spend a lot of time thinking about and

adjusting for confounding, and I think we can do a

pretty good job of that, it is much harder to

adjust for misclassification, and it is essentially

impossible to adjust for bias.

So, I think one of the things we have to

ask about is are there plausible sources of

misclassification and bias, and if there are, in

which direction do they work and would they

seriously change our interpretation.

We talked about the fact that absolute

differences are the important ones that we care

about. We have already started to look at data

that talks about person level risk and population

level risk, so beyond saying that at the end of the

day, I think these are the answers that we really

need to talk about, not about relative risk.

Personally, I think that we need two kinds

of answers. One is what is the information that

patients and their physicians need to have to make

decisions for them personally about whether to

accept certain kinds of treatments in exchange for

certain kinds of anticipated benefits.

I think there is a population level

concern that we have to have that emerges from the

same set of analyses, but takes on a different

form.

So, you will be pleased to know that I am

wrapping it up now, and I would say that both the

cohort and nested case-control designs, which are

the bulk of the observational studies that we are

looking at, are relatively strong ones and I think

deserve the committee's real attention.

I am sorry that not every one of these

studies prespecified a primary hypothesis that we

can attend to, but we should whenever possible do

that. Even though we don't find important effects

in some of these studies, I think it is important

to recognize that they don't exclude one.

As I have said, I am least certain about

attaching great weight to relatively small excess

risks even understanding that when they are

extrapolated to a large population, they could

account for very important public health problems.

Finally, I would say that the things that

support the studies' conclusions are the fact that

when we do subgroup analyses and look for

dose-response effects, that they strengthen the

cause-effect relationship, and I think that there

is reason to look for consistency across studies.

I take the point that was made yesterday

that it is possible that a dozen studies of

naproxen could all have the same underlying bias

that shift the point estimate in the same

direction, but it is not so clear to me what that

bias is.

So, I think that we would have to have a

reasonable idea of what might explain consistent

differences across studies and ask if they are of

sufficient magnitude to explain that. As I say, I

am not clear that there are those kinds of biases.

I think we have to be cautious about the

fact that residual confounding bias and

misclassification are all issues with these

studies. So, I think that while they add to our

discussion, they have to be considered in light of

the fact that they are imperfect vehicles.

Thanks.

(Applause.)

DR. WOOD: Thanks very much.

Let's just go straight on to the next

speaker and then we will take questions for Dr.

Platt after David Graham's talk.

The next speaker is Dr. David Graham from

the FDA.

Review of Epidemiologic Studies on

Cardiovascular Risk with Selected NSAIDs

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

DR. GRAHAM: Good morning. Today, I will

give a review of epidemiologic studies and

cardiovascular risk with selected NSAIDs. I will

be evaluating epidemiologic data from the published

literature plus two currently unpublished studies

that I have evaluated.

My focus will be on providing estimates of

risk of acute myocardial infarction in the setting

of the use of COX-2 selective NSAIDs or naproxen,

although I will have some comments in light of

yesterday's discussion about other NSAIDs on those,

as well.

The methodology was to do a PubMed search

by specific NSAIDs and then cross-check the

citations in those articles to see if there are

other articles I had missed.

I would also like to take this moment to

thank Dr. Crawford for his leadership in making it

possible for me to present some of our preliminary

data from a study in California Medicaid, which Dr.

Gurkiepal Singh from Stanford and I recently

completed.

Before I get into the substance of my

talk, I just want to comment a little bit on excess

cases and projecting to the national population

what was the impact of rofecoxib use, and I am

doing this for two reasons - one, because it has

been a source of controversy and concern. We cite

a number in a paper that I and others have

published from Kaiser Permanente in which we made

an estimate of the impact of rofecoxib use.

Tomorrow, FDA will present its estimation

of the number harmed by rofecoxib, modeling

randomized clinical trial survival curves. A

couple of things I would like the Committee just to

be aware of when they see that data tomorrow. It

assumes a grace period at the beginning of use that

is based on the VIGOR study and the APPROVe, 6-week

grace period in which there is no difference in MI

or increased risk of MI, and the first six weeks of

high-dose use with the first 18 months of low-dose

use of rofecoxib.

As I will show later in my talk, I believe

that this is unreliable due to low statistical

power early on, because we are only talking about

in each of these studies a handful of cases early

on in the study. Two or three cases of MI and wide

confidence intervals, you could have divergence of

the curves very early.

The epi studies, however, that I will

present will show that there is a 3- to 50-fold

more events to work with, more statistical power,

and it suggests a different outcome.

The second is, is that the patient

enrolled in randomized clinical trials are

generally healthier than patients in the real

world. So, if you are going to model what is the

number of people who have been harmed in the

population, you have got to assume what is the

background rate that you are modeling off of.

If you use a background rate from healthy

people to model what is happening in the population

of people who really aren't so healthy, who have a

higher background rate, you will underestimate the

actual population impact.

So, in any event, now on to the substance

of my talk.

The next three slides provide a very dense

overview of the major features of each of the

epidemiologic studies that I reviewed. I am

looking at COX-2 usage in acute myocardial

infarction.

You can see that they are grouped in

several groups. The top three studies I consider

from an epidemiologic perspective to be stronger

studies to have been done better. In terms of the

things that Dr. Platt just talked about, I thought

that these studies were the stronger studies.

The next two studies from the published

literature I thought were less strong, and I will

describe why. Finally, I have separated out these

last two studies, one submitted by Merck to the

FDA, performed by Ingenix, and the other, the

Medi-Cal study that Dr. Gurkiepal Singh and I have

recently completed of unpublished studies, so they

are separated out from the group.

You can see we are talking about different

source populations, and so if we can see

consistency of results across different

populations, different age groups, and different

study designs, I think that that adds support to

the notion that there is a real effect.

If we begin to see that there is a lack of

consistency across the studies, then, many of the

things that Dr. Platt talked about before need to

be considered sort of the individual level of the

studies, so what might explain why one study shows

something and another one doesn't.

This next slide shows the case definitions

and in a number of cases that we were working with

to come up with the relative risk estimates that I

will show you.

All of the studies began with hospitalized

acute myocardial infarction. Several of the

studies were able to link members of their base

cohorts to death certificate data to identify

sudden cardiac deaths, as well. So, those are the

ones that have the +Sudden Cardiac Death.

The asterisk next to the Kimmel study is

to remind me and to remind you that the Kimmel

study was based on nonfatal MIs only. By their

design, they had to interview their cases in

person, so the patient had to survive their

myocardial infarction to be interviewed. So, there

are those differences in study design.

In the end, what is very important in an

epidemiologic study in dealing with this issue I

think in particular, is what is the statistical

power of the study, and that is driven primarily by

the number of events in the exposed group that we

have to deal with.

So, in this column here, you will see the

total number of cases of myocardial infarction that

were identified in each of the studies. The

asterisk next to the Ingenix study 628 is to remind

me that in that study, they identified about 1,700

MIs in total, but they excluded 1,100 of the MIs

because they occurred in people who weren't exposed

to an NSAID at the time of the myocardial

infarction. So, as a result, they left them out,

because in the previous slide, when we look at the

reference group, most of these studies used either

non-use or remote use as the comparator. The

Ingenix study used active treatment with either

diclofenac or ibuprofen.

I would like to say one thing about

reference groups. Dr. Platt brought it up before.

In this issue, I don't believe that there is a

single best or optimal reference group. What you

really want to do is get as close as you can to a

placebo group that has been randomized and has all

the risk factors of the people who are getting the

drug.

In the observational world we can't get

there, and so at the end of the day, if you want to

do a study, you are in a sense forced to pick among

the least evil of that you think, and then it has

to do with how you define things.

So, non-users, for example, could be

viewed as being close to the placebo group, they

are not getting the drug. The problem is people

who don't use drugs tend to be healthier than

people who do use drugs, so that raises a host or

problems.

Yes, we can try to adjust for confounding

and the like, but you are still left with that

concern that they may be, in some way that we can't

measure, different from the people who get the

drug.

In the study I did, and in several other

studies that people have done, we opted to use

people who had been treated with NSAIDs in the

past, but weren't currently taking an NSAID at the

time of the event or the study, the reasoning there

that whatever the selection factors are that lead

to a patient getting an NSAID, that some of those

selection factors are there in people who

previously received NSAIDs.

That is still not a perfect group, though,

because you could argue that patients who are no

longer taking NSAIDs might be healthier than people

who are currently taking NSAIDs.

Finally, the problem that is posed by

using an active comparator. If you have an active

comparator, and I am comparing another drug to an

active comparator, and I see a difference, I don't

know what it means. I need some place to anchor

the result, and for that reason, although none of

them are perfect, I believe that the non-use and

the remote use analyses at least give us a way of

pegging results, and if we want to compare one drug

to another drug, if we had that common reference

point, at least it allows us to accomplish that.

The one other thing I would like to point

out about the number of cases is that for

rofecoxib, especially at the high doses of

rofecoxib, most of these studies had relatively few

exposed cases. The exception is the California

Medicaid study where we had 157 exposed cases to

the higher dose of rofecoxib.

Now, this is a very busy slide and I won't

spend a lot of time going over it, but I will be

happy to answer questions later.

Basically, before we heard there are

unmeasured risk factors in automated databases that

frequently can't be accounted for, aspirin use and

smoking are among the most common. So, you can see

here that most of these studies, that information

isn't obtainable.

Kimmel was able to get both because they

interviewed the patients, the cases and the

controls. In the Medi-Cal study, it turns out that

aspirin is reimbursed, and so we have a handle on

it there.

In the Graham study, a survey of controls

was done to see what these unmeasured factors might

look like in the source population. The Solomon

study did the same thing, relying on the Medicare

Beneficiary Survey that Dr. Platt talked about

before.

Important limitations I think that need to

be highlighted are that in the Mamdani study, they

excluded patients who had less than 30 days of

NSAID use, so the survivor bias Dr. Platt talked

about before, in my view, is big concern with this

study, and for that reason I ranked it in sort of

that category of low quality studies.

In the Kimmel study, as Dr. Platt also

mentioned, there was low participation rate.

Basically, half of the cases and half of the

controls who approached volunteered to be in the

study. More importantly I think in that study, and

it's unfortunate, is that there was what I would

refer to as the potential for, in quote "reverse

recall bias."

Normally, with recall bias, we think oh, I

have had a heart attack, I am going to remember

more efficiently what happened to me immediately

before the heart attack compared to some control

where I say to the control what were you doing four

months ago on this particular day.

That is the classic recall bias. This

situation I think had what I would describe as

reverse recall bias. They interviewed the people

who had heart attacks within four months of getting

out of the hospital - what happened to you the day

and the week before you had your heart attack four

months ago.

For the controls, they call them on the

phone and they way what happened to you yesterday

and the week before, so it is actually the reverse.

The controls actually would have better recall of

what they were actually doing than the cases

potentially, and we will see how this is reflected

in some of the results.

Finally, with the Medi-Cal study, I think

the single greatest concern for the committee in

considering these data (a) that it is preliminary

data, and (b) that this is a new database for

research purposes.

For that reason, I am just including a

slide to orient people to that. The other

databases are ones that have been used before.

This is a database that only in the last two years

has come online to be sort of a quality sufficient

to begin contemplating doing studies.

Its strengths are that it is very large,

it captures aspirin use, it doesn't censor people

by age. It combines Medicare coverage when you go

over the age of 65 with the prescription benefits

of Medicaid, so you get the drugs and the outcomes.

Matching has been done to multiple cause

of death tape, so that we have death data in this

database up through 2002. We didn't include it in

the data I will show today because we really want

the information up through 2004.

Once people get into Medicaid or Medicare,

they don't tend to drop out. The limitations are

that we can't get medical records, and that is

something to understand, and that is a very

complicated database. Dr. Singh from Stanford who

is the principal investigator for our Medi-Cal

work, and who has worked to bring this database

online, spent two years putting things together and

working out the kinks in it before contemplating

doing research with it, so at least you understand

the limitations of that.

There is always the concern about

unmeasured risk factors and Dr. Platt talked about

that. I want to review for you very briefly some

of the evidence from the published literature where

efforts were made to look at what unmeasured

confounding looked like and did it differ across

NSAID type.

In our study using Kaiser Permanente data,

we did a survey, a random survey of random sample

of controls, and we looked at aspirin use, smoking,

and over-the-counter NSAID use. You say see by

NSAID that there really was not significant or

substantial differences in the distribution of

these risk factors.

So, if they don't vary in the control

group, they can't really confound that observation

that you see very much.

In the Solomon study, these are the data

from the beneficiary survey. Dr. Platt already

mentioned a further analyses of these data that

showed that the actual impact of all these

unmeasured confounders on the measure of the

relative risk at the end was measured in the

hundredths of an odds ratio, so if the odds ratio

was 1.34, adjusting for these things and projecting

it out would change it to maybe 1.35 or 1.33. We

are talking about minuscule differences, not

qualitatively important differences.

Finally, in the Kimmel study, they also,

through their interview, were able to see that for

most of these factors, there was similarity across

NSAID groups except for current smoking where the

rofecoxib group had much lower current smoking than

any of the other NSAID groups, but for past

smoking, it was more than the other NSAID groups or

the remote groups, and if you added these two

together, the rofecoxib was very similar to these,

but the celecoxib group had more smoking.

My own conclusion from this is that yes,

it is possible that some of these unmeasured risk

factors could be influencing the results. I don't

think that there is strong evidence that there is a

systemic bias that would sort of lead to

interfering with trusting the results and thinking

that these factors are confounding the observations

that we see.

So, first, I will talk about rofecoxib,

then I will talk about celecoxib, then I will talk

about valdecoxib in terms of epidemiologic data.

These studies on the left, with their

reference groups, are the ones that looked at

myocardial infarction with rofecoxib. What I have

shown is for all doses and where it was present

less than or equal to 25 milligrams and over 25

milligrams, what the fully adjusted odds ratio and

95 percent confidence intervals were.

These studies varied in the extent of

adjustment that they did. The Ray and the Graham

studies each adjusted for about 30 cardiovascular

risk factors. The Solomon study was a somewhat

smaller number, Mamdani was a somewhat smaller

number. Kimmel, they adjusted for somewhere in the

20s, the Ingenix study somewhere in the 20s, the

Medi-Cal study adjusted for about 40 cardiovascular

risk factors.

What you can see is when you look across

the All Doses is that, in general, the point

estimates were elevated and for many the 95 percent

confidence intervals excluded 1.

More importantly, though, is looking at

the low dose and the high dose data because we know

from the clinical trials data, and we would suspect

it on just pharmacologic grounds, that if there is

an association that it might be worse with the

higher dose than with the lower.

So, four studies provide us estimates at

the low and the high doses, the Wayne Ray study and

our study from California Medicaid, and then the

two unpublished studies, one from Ingenix and the

other from California Medicaid.

We see there that in three of the four

studies, there is an elevation in the point

estimate. In the Graham study, it included one.

When we look over 25 mg, we see greater consistency

although in the Ingenix study, there is this

paradoxical finding of sort of basically a neutral

relative risk. I don't have an explanation for why

that happened, but it makes me concerned to some

extent about what was going on in that study,

because it is a result that goes in a very

unexpected direction.

What I would like to point out, because I

will come back to it again, is that when we are

dealing with drug safety, and the goal now is what

risk can I exclude, if my job is--now I am not

talking about efficacy anymore, what I am talking

about is safety--if my job is to protect the public

from harm, what risk can I exclude based on the

data that I have, I believe that is much more

relevant to look at the upper bound of the

confidence interval than the lower bound.

What traditionally happens is we look at

the lower bound of the confidence interval and we

say if it includes one, there isn't a problem, but

the biggest reason, as Dr. Platt showed in his

previous slide, for a wide distribution and a wide

confidence interval in your study, is that the

study doesn't have enough statistical power to get

you a narrow enough confidence interval to say that

you have the 95 percent certainty that you want.

So, if your mission is above all else I

want to do no harm, that I want to protect patients

from harm, then, based on the data you have, I

would submit that the upper bound of the confidence

interval provides greater assurance to patients,

and then if you are going to compare a benefit to a

drug, that you might want to consider that benefit

against that upper bound of the confidence

interval, because that is compatible with the data.

In any event, that is my view, and not the FDA's.

This is a slide from California Medicaid.

It is preliminary data and I wanted to present it

to you, because what it shows is a dose-response to

rofecoxib from 12.5 mg up to and through 50 mg.

You can see that we have very wide

confidence intervals for some of them, and that is

a reflection of the limited number of cases, but I

want to point your attention to the very narrow

confidence intervals in the 12 to 25 mg and in the

25 to 50 mg, just to point out that in the previous

slide here, where we are talking about what are

these point estimates, that now you can what we

have done is we have fleshed them out a little bit

more.

Another comparison that I think is

important to consider, certainly it was for us,

when we did our study in Kaiser Permanente, was at

the time there were two COX-2 selective inhibitors

on the market, celecoxib and rofecoxib.

The bigger study raised a question about

high-dose rofecoxib. Our question as researchers

was, and public health scientists, was, well, let's

suppose that rofecoxib increases the risk of

myocardial infarction.

We don't know that it does, but let's

suppose that it does, what about celecoxib, because

it actually had a larger share of the market, and

if it turned out that these drugs have a benefit,

and that benefit is worthwhile, then, it would make

more sense from a practical perspective to use the

drug that had a better safety profile.

So, to us, it was very natural to want to

compare rofecoxib to celecoxib, and so several of

the epidemiologic studies felt similarly and in

their design they included that analysis, and some

of them it was, as Dr. Platt said, part of a we are

going to make comparisons of everything against

everything.

The Solomon study, for example, did that.

They did not state in that study what their prior

hypothesis was. In our study, we did state it. I

mean yes, in a sense we had multiple comparisons,

but we were interested in two different things. We

were interested in rofecoxib versus remote use, and

we were interested in rofecoxib versus celecoxib,

but we thought it beforehand and we planned that

analysis.

But in any event, what we say is, when you

look at the all dose analysis, in all of the

published studies, rofecoxib increased the risk

compared to celecoxib. When we looked at low dose

rofecoxib, we see the increased risk. When we look

at the high doses of rofecoxib to celecoxib, again,

we see the same pattern.

Dr. Platt, in his talk before, talked

about relative risks, risk differences, individual

risk, and population risk. The next two slides are

intended to address this at the level of the

individual and at the level of population.

What I have done on this slide--and these

slides now, no one should interpret this as meaning

this is what actually happened in the

population--the next slide is going to have numbers

on it that are for illustrative purposes only, to

help the committee understand what does a relative

risk of 1.3 translate into at the individual level

and at the level of population.

Your typical COX-2 user is somebody in

their 60s who has several other health problems, so

I went to the National Center for Health Statistics

and got the myocardial infarction rate for 65- to

74-year-old men in the United States. That rate

turns out to be 1 per 50 per year.

What I did is I took that as the

background rate and I said if I have an individual

using this drug with that background rate and then

I applied to that person the relative risks or odds

ratios found in these studies that are shown in the

previous slides, what would the excess risk to the

person be, sort of what would that risk difference

translate to for the individual.

For example, in the Ray study, if you

remember, for 25 mg or less, the odds ratio was

1.02. Basically, it doesn't change. If we based

it on the point estimate, that 0.02 would translate

to 1 out of 2,500 in a year increased risk of heart

attack.

Another way to view that number is, is

that is the number needed to harm. If I treated

2,500 65- to 74-year-old men for a year with

rofecoxib, and the rate was 1.02 that Ray found,

treating 2,500 patients would produce 1 extra heart

attack.

Now, with the other studies that found

higher estimates for the lower doses of rofecoxib,

you can see that the number needed to harm ranges

from about 90 to 200. That is saying for every 90

people to every 200 people I treat with low-dose

rofecoxib, I would generate 1 other case.

For high doses, because the relative risks

were higher, the number needed to harm becomes

lower.

I have also shown it based on the upper

bound of 95 percent confidence interval to show you

that based on the data we have at hand, these are

the excess risks that are consistent with the data,

and from a public policy perspective, from a public

health perspective, that is what I react to, and

when I want to see a benefit and say does benefit

exceed the risks, well, I want to know what is a

real benefit in the population in terms of reduced

hospitalization, lives saved, and does that benefit

exceed what I can say is possibly the risk of these

products.

At the population level, now we have gone

from an individual. Remember in the Wayne Ray

study we said it is 1 out of 2,500. Well, that

would translate to 400 additional cases of heart

attack if we treated a million men who were 65 to

74 years old, and we treated them with rofecoxib

low dose for a year.

With the others, you can see that those

relative risks that might not look so impressive,

that 1.23, that 1.30, that 1.4, that it projects

out to a substantial number when you multiply it by

the large number of people who use these products.

For high doses it ends up being even

greater, and then if we focus on the upper bound of

the confidence interval, we again see that the

numbers are larger still. This very high number in

our study was the result of our having low

statistical power in addressing the high dose

rofecoxib.

One other question that I think is

important to consider is when does the risk of

myocardial infarction with rofecoxib kick in. Now,

we have seen data yesterday presented by both FDA

and by Merck of various survival curves.

We saw the bigger curve that showed the

separation after about 6 weeks with an overall

relative risk of about 5. We saw, for the APPROVe

study, this close overlapping line at about 18

months, and then they diverge with an overall

composite hazard ratio of about 2.

I would submit to the committee that the

reason for the failure of these studies to show

divergence of the line shortly after the drugs are

used are low statistical power, that they just

don't have enough events to show it, and as a

result, you can interpret because of the low

statistical power you basically--how to describe

it--you presume that there is nothing there, and

you err on the side of the drug rather than erring

on the side of what could the risk be to the

population.

If you really want to know what is going

on in the population, then, you want to reduce the

uncertainty. The more uncertainty you have, if you

act basically on the lower bound of that confidence

interval, which is what you are doing when you are

saying the risk doesn't begin until 18 months, you

are basically saying that the absence of evidence

is evidence of absence.

I would say that in safety, what it is, is

you just don't have enough power.

Looking at the epidemiologic studies, I

think that we have evidence to suggest that the

risk begins much earlier. I will point it out, and

you guys and women can consider it for yourselves.

In the Graham study, when we looked at low

dose and high doses of rofecoxib, 50 percent of our

cases at the low dose and at the high dose had used

at the time--remember these are inception cohorts,

so these people, their total use, this was 1.8

months, this was 2.7 months--50 percent of our

cases occurred within 2 to 3 months of starting the

drug.

That is a lot of power and that really

speaks against the notion that the risk is

backloaded, you know, it is for the low dose, that

the risk doesn't happen until after 18 months.

Nobody in our study was on rofecoxib for more than

about 15 months. I think that was the longest

duration of use we had in our study.

Now, in the Solomon study, they looked at

the low dose and the high dose, and they presented

data in several ways. One is that they grouped

things in 1 to 90 days, and what they showed was

that for both the low dose and the high dose, there

was evidence or risk early on.

The Kimmel study, for all its

deficiencies, most of it was low dose rofecoxib,

and almost all the patients used it for less than

12 months. So, their finding on rofecoxib, if

anything, would also speak to that the low dose

effect kicks in long before 18 months.

Finally, the Solomon and the Ingenix study

looked at the first 30 days of use of these

products, and both of them found elevated odds

ratios of 4 for cardiovascular risk in the first 30

days.

Now, in both of these studies, they didn't

separate it out by low dose and high dose, so this

is a composite, but in both studies, about 85

percent of the use to 90 percent of the use was low

dose.

So, basically, what I am concluding from

this slide is that risk of myocardial infarction

with rofecoxib begins when rofecoxib use begins,

and that the inability to separate out those curves

is based on the fact that if you were to count the

actual number of events in the bigger study in the

first 6 weeks, we are probably talking about 3 or 4

events, and if you look at the confidence

intervals, you are going to see they are wide.

For the APPROVe study, the same thing

holds, that you have too few events. The whole

study had 45 events, and I don't recall how many of

those were on rofecoxib and how much of those were

on placebo, but when you think about it, compare

that and then look at the epidemiologic studies,

and look at the number of cases that were in the

epidemiologic studies, and for all their problems,

and we can talk about those, they suggest there is

a big discordance, and I think the answer, the

reason is absence of statistical power in the

clinical trials.

In the epidemiologic literature, this has

been recognized, and people have written papers

saying that when you are trying to summarize the

overall risk from a survival study, and you want to

look at specific time periods, that you are better

off taking the overall risk estimate for the entire

study than focusing on a small segment at a time

because of this issue of low statistical power, so

I didn't invent this.

Now, switch over to celecoxib. There are

a number of studies that have been done to look at

celecoxib risk. What I have tried to do here is

plot out for you the relative risk or the odds

ratio, the author of the study, and then the point

estimates in the 95 percent confidence intervals.

What you will see basically is that for

most of these studies, there is no evidence of a

protective or an injurious effect except for the

Kimmel study that found a substantial protective

effect.

Remember the Kimmel study and what I

believe is this reverse recall bias, as well as the

low participation rate, and I personally discount

that study. The committee can decide for

themselves that they want to do.

What about celecoxib lower dose versus

higher dose? Well, unfortunately, the only place

where this is adjusted, is looked at are in the two

unpublished studies. We have the Ingenix study and

we have the Medi-Cal study.

What I would focus your attention on are

the low dose and high dose, the low dose and the

high dose. What we see is in both studies,

evidence of a dose response. Now, the 95 percent

confidence interval in the Ingenix study includes

1, but the point estimate is pretty elevated. That

is 1.18 or so at 400 mg.

In the Medi-Cal study, we go from 1.01 up

to about 1.24. Here, you can see the 95 percent

confidence intervals.

What I would conclude from this, although

they are unpublished studies, that there is

evidence of a dose response at the higher doses of

celecoxib do confer an increased risk of myocardial

infarction.

I should point out that in the Medi-Cal

study, the methodology that we used in that study

is the exact methodology that we used in our Kaiser

Permanente study that Dr. Platt before was gracious

enough to say is one of the better done studies.

There are no published studies on

valdecoxib, so what do we do? Well, preliminary

data from Medi-Cal, we had 54 exposed cases and we

found a point estimate of 0.99. Now, this was

mostly 10 and 20 mg use. I think that out of all

the patients that we had in the study, there were 2

or 3 who had 40 mg valdecoxib use.

In Medi-Cal, they only reimburse for the

10-mg tablet, and they do this in an effort to try

to discourage people having larger dose tablets and

then taking more of it.

So, this is all the epidemiologic

information that I am aware of, that I have had an

opportunity to review on valdecoxib.

I will now move to naproxen. The issue of

naproxen is important for several reasons. One,

with the VIGOR study, the medical community was

confronted with the hypothesis that naproxen was

the single greatest and most effective

cardio-protectant in the history of mankind, that

it was far better than aspirin.

We heard yesterday that aspirin reduces

cardiovascular risk about 20 to 25 percent.

Naproxen, if we were going to believe the VIGOR

results, would have to reduce the risk of

cardiovascular events by about 80 to 85 percent.

So, this stimulated a lot of research.

Here, I have summarized in the same fashion as I

did for the rofecoxib studies, the various studies

that have been done. Again, I have separated them

out by the studies that I think are better done,

the studies that have more significant limitations,

and then the two unpublished studies.

I point out the Rahme study to say that

the only reason the Rahme study is listed among

this group of suboptimal studies is that its

reference group was other NSAIDs, primarily

ibuprofen, because ibuprofen was the predominant

other NSAID used in Quebec during the study.

Again, we have the various outcomes that

were done. What I would point is that you can see

the number of cases that we had to work with in

these various studies, and I would point out that

for the Solomon study, they had about 240 MI cases

that they studied overall, but as you will see in a

few minutes, that exposure could occur anytime in

the past 6 months, so they don't see in the paper

how many people were actually on naproxen at the

time they had their event, so I can't put down a

list of how many people were currently exposed.

The Watson study is the only study that

used a composite outcome. It included myocardial

infarction, stroke, subarachnoid hemorrhage, and

subdural hematoma. Why subarachnoid hemorrhage and

subdural hematomas are in there is beyond me. In

any event, 26 cases of that composite outcome and a

much smaller number of actual myocardial

infarctions. So, that is why that asterisk is

there.

With the Ingenix study, the asterisk next

to the 179 is that this included both prevalent and

incident cases, and the best studies, the best

results come if you base it on incident cases only

or incident use only as opposed to prevalent use,

because prevalent use can have survivor bias. But

in any event, in the Ingenix study, they had a

number of different analyses, and they didn't

always use their full number of cases.

There are important limitations to note.

I think the one to focus is to realize (a) there is

no perfect study, we have talked about that before,

and, two, that among all the limitations listed

here, I think the most important one to note was in

the Watson study, was this composite outcome which

really just makes it very difficult from an

epidemiologic perspective to study things.

Myocardial infarction is very well

validated in claims data, and Dr. Platt has already

gone over that with you. Stroke is notoriously

difficult to work with in claims data, and subdural

hematomas most commonly occur because as people get

older, their brains shrink. They bump their heads

and then they get a little bleeding on the surface

of the brain. What that has to do with myocardial

infarction risk, which is what we are really

concerned about today, is beyond me.

I have got two slides on the results.

This slide shows the studies that found no

protective effect. There is four studies that

found a protective effect, and I am saving them for

a separate slide, because I want to look at those

individually.

What you can see from the majority of

these studies, and I would point out that the

studies that were the best done studies in the top

tier, they are on this slide, that all of them sort

of suggest that there is no cardio-protective

effect of naproxen. Several of the studies point

to the possibility of a small increased risk with

naproxen.

But we have four studies of positive

results, and we will probably all remember the

Archives of Internal Medicine publishing three of

the articles in the same issue with an accompanying

editorial that stated the issue is solved, naproxen

is cardio-protective.

I want to look at those studies and just

describe to you my view of them. The top three

studies were the ones that were--well, no, not the

Kimmel study--Rahme, Solomon, and Watson were the

Archive studies.

In the Rahme study done in Quebec, they

compared current naproxen use versus other NSAIDs.

That other NSAID was, by and large, ibuprofen, and

they found a protective effect. Well, if ibuprofen

increases the risk of myocardial infarction, let's

just say that it does, and naproxen doesn't,

naproxen could look like it's protective compared

to ibuprofen, but not be protective really.

The data presented in that paper, if we

re-analyzed it versus non-use, we get an odds ratio

of 1.28, statistically significant. Now, this is

not adjusted. It is not possible from the data

there for me to adjust this result, but based on

what is in the paper, when you compared the

unadjusted to the adjusted point estimates, they

don't change very much, and what that suggests to

me is that this effect, this 0.128 is probably not

far off the mark.

That would then make it comparable to the

analyses I showed on the previous slide, that all

of these slides use non-use or remote use, so then

it would add a fourth study to an elevated point

estimate for naproxen.

Now, the Kimmel study, we have already

talked about low participation rate and this

reverse recall bias, and a small number of NSAID

cases. In fact, they don't even tell us in the

paper how many cases they had.

We move on to the Solomon study. This was

the result that was reported in the paper and was

picked up by the press, a 16 percent reduction in

heart attack risk with naproxen. The problem, in

my view, was that their definition of exposure in

the study was any use of naproxen in the past 6

months, which means that if I took naproxen 6

months ago and stopped it, I could be included in

this study as being exposed to naproxen.

So, the question is then, you know, how do

we interpret the study. Well, Solomon was good

enough to present data by current use and in recent

use, and recent use included people who stopped

their naproxen. Their naproxen prescriptions day

supply ran out between 1 day and 60 days before the

MI or the index date for their controls, and remote

users, their NSAID use, their naproxen use ended

from 61 days to 180 days prior to the event.

So, let's look at what those results are

then, and what we see is they are identical. So,

unless the committee is prepared to believe that

naproxen confers lifetime immunity to

cardiovascular disease, I think we have to conclude

from these data that what we really have here is

selection bias, and it is not the fault of the

investigator. Dr. Platt talked about before that

there are some things you can't adjust for. You

can't adjust for bias. What you can try to do is

identify bias, and if you identify it, then at

least you know what you are dealing with.

Here, I think we have what is classic

selection bias. It is not naproxen that protects

you again myocardial infarction, it is some other

factor that in this health plan, that they used to

study this drug, the patients who were being

treated with naproxen happened to have lower

cardiovascular risk.

I can't explain why that happened. Dr.

Solomon probably can't explain why it happened, but

it's not due to naproxen.

Finally, the Watson study. This study was

sponsored by Merck, and it was authored by Merck

investigators. The result that was published as

being the basis for the conclusion was this top

result, a 39 percent reduction in cardiovascular

risk.

First, I just want to remind everybody,

composite outcome here, subarachnoid hemorrhage,

subdural hematoma, stroke, as well as heart attack,

26 events total, much smaller number of heart

attacks.

For this event, you can see the

checkmarks. These are the various variables that

they adjusted for in the study. The way they

handed cardiovascular risk, if you read the paper,

I would have to say that it doesn't measure up to

the standards that were set by Dr. Wayne Ray.

We modeled our study in Kaiser and in

Medi-Cal, and Dr. Wayne Ray, I think that he has

set the standard for how one needs to go about

adjusting for cardiovascular risk. It is not enough

to rely on diagnoses. You have to use the

medications, because medications are much more

accurate predictors of disease than diagnoses in

these administrative claims data.

In any event, they didn't adjust for

cardiovascular risk, and they didn't adjust for

smoking although they had that data. Then, they

present later on another analysis that now includes

cardiovascular risk and it is no longer, in quotes,

"statistically significant," and then they include

smoking, and again it is not statistically

significant.

My conclusion on the Watson study was that

(a) they have got a composite outcome that, in my

view, isn't very informative towards the question

of myocardial infarction; (2) that it is very small

numbers; (3) that a variety of approaches were used

in the analysis that inadequately account for the

risk factors that could confound the result, so I

have discounted that, as well.

So, a conclusion when I look at these, in

quotes, "4 positive studies," I conclude that none

of them provide credible evidence of a protective

effect.

In light of yesterday's discussion in the

afternoon about other NSAIDs and what might explain

the differences, let's say, celecoxib and rofecoxib

studies, the rofecoxib studies used naproxen as a

background, a comparator, the celecoxib studies

using ibuprofen or diclofenac.

Dr. FitzGerald is talking and saying,

well, you know, all of these drugs could increase

the risk because what is happening, you know,

biochemically, with the balance of prostacyclin,

could be influenced by these different drugs in

ways that aren't immediately obvious or detectable

in a clinical trial.

I thought I would just share some of that

information on other NSAIDs with the committee,

recognizing a couple things that no single study is

definitive and what you want to look for I think is

consistency across studies, but as far as

randomized trials go, I would like just to mention

that there are generally too small, too few events,

and you are not going to get the answers that you

need from them unless you make these clinical

trials substantially larger than anything people

have contemplated up to now.

So, from our California Medicaid study, it

is all preliminary and it has not been published,

for ibuprofen we found a small but statistically

significant increased risk. For indomethacin we

found a risk of 1.7. I would like to say on

indomethacin that we found an increased risk with

indomethacin in our Kaiser Permanente study. It

was 1.3 and it was highly statistically

significant.

In at least two other studies that I

reviewed in preparation for this advisory meeting,

indomethacin is noted to have an increased risk of

myocardial infarction.

It is not commented on in the text because

that wasn't a primary analysis, but what I am

talking to you about now is consistency, and I

would submit to the committee that indomethacin is

a lot of smoke, there is a lot of smoke for

indomethacin.

In our study, in our Kaiser study, for

example, we did not think in advance to look at

indomethacin separately. I mean we knew we were

going to look at it, but it wasn't a primary

hypothesis. We didn't adjust for gout. I mean

everyone knows that indomethacin gets used in gout.

Gout increases the risk of cardiovascular disease.

Well, in the Medi-Cal study, we adjusted

for gout. Yes, gout increases the risk of

myocardial infarction. It didn't change the odds

ratio here.

I think this next finding, Meloxicam, is

important. Meloxicam is now the number one selling

branded NSAID in the country. With the removal

from the market of rofecoxib, the medical

community, shying away from the coxibs, are moving

to other drugs that they perceive would have the

advantages of COX-2 selectivity without the bad rep

that coxibs appear to be acquiring.

So, you now have a shift in the

marketplace to Meloxicam. There have been articles

in the Wall Street Journal and the New York Times

on this. The company recently raised the price on

the tablets.

In any event, we are presenting these data

just to say that we found an increased risk. It is

one study, but I think it is the only study. We

looked at this in Kaiser. Meloxicam is almost not

used in Kaiser, so we couldn't study it.

In our California Medicaid study, we only

looked at drugs that had more than 50 currently

exposed cases. Nabumetone came out in this study

as not showing a whiff of a problem. Sulindac,

there was an increased risk.

Regarding ibuprofen, in our Kaiser study,

we found an increased of 1.06, which sounds really

trivial. It wasn't statistically significant, but

the confidence intervals were pretty narrow. It

was 0.96 to 1.17.

My concern is, as Dr. Platt talked about,

you know, above 2 you feel really comfortable,

above 1.5, you can believe it, below that you begin

to get really edgy. The problem is most of the

risks that we are probably facing, if it turns out

that the non-coxib NSAIDs increase the risk of

cardiovascular disease, that is where the risk

level is going to be, and that is what we are going

to have to contend with, because it has tremendous

effects on the population.

Finally, dose response. This slide shows

for diclofenac. This is from California Medicaid.

What we wanted to do was show evidence of dose

response, consistency in the data. Remember we

pointed out diclofenac before. Diclofenac in this

study overall did not have an increased risk, but

at the high doses there is a suggestion of a dose

response.

I will skip that. This slide was to say

that depending on your reference point, you can get

different results, if I use an active comparator

versus remote, and this is showing the three NSAIDs

from California Medicaid compared to non-coxib

NSAIDs, and you can see the rofecoxib is different

than them, and the other two aren't necessarily

that different.

My conclusions, and I am sorry to have

gone so long. Celecoxib, we believe that based on

the evidence we have at hand, that there is no

apparent effect of risk at doses of 200 mg or less.

Above 200 mg, we think that there is evidence of

increased risk.

For rofecoxib, we believe that there is

evidence of increased risk at both the lower doses

and the higher doses, and that risk begin early in

therapy and is apparent during the first 30 days of

use.

With valdecoxib, there is a paucity of

information, but the information we have at this

time suggests that the risk is not increased at

doses of 20 mg or less.

As a class, non-coxib NSAIDs may increase

the risk with differences between each of the

NSAIDs. I don't think we are going to be able to

talk so much about class effects. In the end, it is

going to have to be looking at individual drugs.

The COX-2 hypothesis may be true, but if

it is, we are still going to have to look at these

other drugs in terms of their individual properties

and what they do.

Finally, naproxen is not

cardio-protective.

Thank you.

(Applause.)

DR. WOOD: Thanks very much. David, it

will come as no surprise to you that every time

practically I pick up a newspaper, I read about

what you are not going to tell us.

So, my question to you is what have you

not told us that you think we should know, because

I would like to make sure. Lots of other people

have shown up here without slides that they forgot,

so I just want to be sure that if there is anything

else we need to hear, we hear it.

DR. GRAHAM: Well, as far as the science

goes, I think I presented the evidence that I am

happy to be able to share with the committee that I

thought it was important for the committee to have

an opportunity to hear.

The source of controversy surrounding my

presentation related to the unpublished studies

that I was going to be permitted to present or

asked, actually asked to present the Ingenix

results, the unpublished study from Merck, but that

I was being told not to present the unpublished

data from the California Medicaid study, and

personally, I had great difficult standing here

before this committee as an investigator and as a

scientist, as a physician, and telling you the

information that I have, that I am allowed to talk

about, and remaining silent on things that I know

about that I am not allowed to talk to you about.

Fortunately, Dr. Crawford exercised great

leadership in making it possible for me to present

that data, recognizing it's preliminary, but the

methods that we used are identical to our Kaiser

study for the California Medicaid, and for me, I

think the big reservation is, is that it's an

untested database, but I think that everything that

could be done to develop the database and to do

quality assurance and to work out the kinks has

been done.

If you look at the findings in the

California Medicaid study and you compare them to

the clinical trials data, and the anomalies and the

questions that you were discussing yesterday about

the clinical trials' data, you look back at the

California Medicaid data, and you are going to see

I think great consistency between the findings that

might help explain and interpret some of the things

that seemed questionable or uncertain yesterday.

So, in any event, I have been able to

present what I thought was important to present,

and I am happy to have had that opportunity.

DR. WOOD: So, the answer is we have seen

it all, is that right?

DR. GRAHAM: You have seen it all.

DR. WOOD: Okay, good. Let me ask you a

question. If you go back to your slide that showed

the excess population risk, put that in proportion

for us in terms of, say, the other drugs that have

been withdrawn from the market. I mean what sort

of numbers would we be expected to see?

DR. GRAHAM: That is a great question.

The typical drug that has come off the market in

the United States, like the leading cause of drug

withdrawals in the United States in the last 20

years has probably been acute liver failure.

Rezulin came off the market because of it,

troglitazone, bromfenac, a number of other drugs.

Acute liver failure in the general

population has a background rate of about 1 per

million per year. We are talking about that is the

rate of being struck by lightning, 1 per million

per year, and these drugs were pulled off the

market because it increased the risk of that. It

might increase the risk 5-fold, it might increase

the risk 10-fold, it might increase the risk

100-fold. The fact is the background rate was 1 in

a million and what that means is that the actual

number of people affected is sort of measured in

the tens and the hundreds for the liver failure

that could be life-threatening.

In this situation, and this is why the

lower relative risk becomes so critical, we are

talking about a serious event that has a very high

background rate. Heart attack is not a rare event,

and as I pointed out before, there is a 1 in 50

chance that the average American male age 65 to 74

is going to have a heart attack this year, 1 in 50.

That is an extraordinarily high risk. You

increase that risk 5-fold with a high dose. That

is what happened with VIGOR. If I have got

millions of people taking the high doses, and that

is what had in the United States, and I have

increased the risk 5-fold, you are going to get

numbers that balloon out like this.

So, there is no comparison in terms of

what the population impact is of the typical drug

that has come off the market in the United States

and what we are dealing with here, and that is

because of the high background rate of the

underlying event that we are talking about.

DR. WOOD: So, this would produce many

more cases from what I understand.

DR. GRAHAM: Many more.

Committee Questions to Speakers

DR. WOOD: From the committee, we have

questions. Let's start with Dr. Shafer.

DR. SHAFER: Dr. Graham, tomorrow we are

going to be asked, as a committee, to consider the

question about a class effect for the selective

COX-2 antagonists and for the non-selective NSAIDs.

One of the things that I am finding, that

I am having trouble putting together here, is we

have a lot of conflicting data, and for the COX-2

antagonists we have a lot of data from randomized

controlled trials.

Certainly for the NSAIDs, we are going to

have to go with a lot of these observational

studies because we don't have a lot of data on the

topic at hand from randomized controlled trials.

As I look at this, if we come up with some

sort of common warning as a class, and it applies

to everything, we have, in fact, communicated no

relevant information. On the other hand, if we are

going to come up with individual drug-specific

recommendations, we are going to have to have very

different evidentiary standards in some ways,

because for some of these, we have very little

information, as you pointed out, and yet your data,

particularly the unpublished data from the Medi-Cal

trial, and I appreciate that there is all the

issues of not being previewed and stuff, but we are

all familiar with that process and know how it

works.

What can you tell us to guide us? Should

we try to go drug by drug specific? How do we set

our evidentiary standards when we talk about class

effects where in some cases, we are just not going

to have a lot of data here?

DR. GRAHAM: Right. What you are going to

be getting now, of course, is my opinion, not FDA's

opinion. Probably if you were to talk to Bob Temple

or John Jenkins, or anybody else, everybody is

going to have a slightly different answer.

What we talking about now I think to some

extent is philosophy, so what that preamble, first,

I believe based on the evidence that there is a

COX-2 effect and that that COX-2 effect is dose

dependent, and that we see evidence of that with

rofecoxib, with celecoxib, and with valdecoxib.

The difference between rofecoxib and the

other two coxibs on the market is that a safe dose

for rofecoxib wasn't identified, the dose wasn't

low enough. That raises a question in my mind

about what is an appropriate therapeutic index for

a drug.

I am giving you my opinion now, but when I

listened to Dr. Cryer's presentation yesterday, the

bottom line conclusion I came to at the end of that

was there really doesn't appear to be a need for

COX-2 selective NSAIDs based on what I heard

yesterday. There is probably other information out

there why I am wrong, but that was the conclusion I

came from.

So, in any event, that is answer one. I

believe there is an effect and it's dose related,

and with celecoxib and valdecoxib, I think we have

evidence. You said before we have a good

evidentiary base based on clinical trials for the

COX-2s. I would challenge that in the sense of the

survival curves and the things that I talked about

there, that we have a very weak evidentiary base

for things like protective, you know, is there a

grace period for use, and also on the dose issue,

we really don't have a great evidentiary base. But

that being said, you understand me.

Now, for the non-coxib NSAIDs, my own view

is that as an epidemiologist first, I try to report

the phenomenon I observe and leave it to brighter

minds to figure out why what I observed happens.

You are asking me sort of what do I think

is happening underneath it all. I am attracted to

the COX-2 hypothesis personally. Dr. Gurkiepal

Singh, my colleague and co-author in Medi-Cal, he

has a different view on that, but I think that we

can these in vitro tests that say, oh, this is the

COX-2 selectivity of this NSAID, you know, in a

test tube.

What happens in the human body could end

up being surprisingly different. We saw yesterday

that the dynamic response of these differences,

that the platelet effect is very quick, the

thromboxane effect is a very quick effect, the

prostacyclin effect seems to be a more gradual

effect, that this creates very complex interactions

that ibuprofen, that any of these drugs could, in

the end, end up with a deficit, a prostacyclin

deficit that results.

I think Dr. FitzGerald showed that slide

yesterday with the normal distribution of the time

area under the curve and then this little sliver

where they are not protected, and that may be the

reason why, for these different drugs, that we end

up with these different relative risks and these

different odds ratios.

In the end, for the non-selective NSAIDs,

my own advice would be let's look to see are there

somewhere in studies--it is going to be

observational studies--in observational studies

that we believe have been reasonably well done.

By "well done," here, they have to be

large. The literature is full of really small

studies. I mean I could have presented Meloxicam

studies, 5 patients, no risk. Well, da, you know,

you have got a confidence interval that goes from

zero to infinity. They need to be large. Look in

a systematic way to identify what the body of

evidence is.

Can we identify bad actors? I believe

indomethacin, for example, is clearly a bad actor,

and if people looking at the data concluded that,

take appropriate action, weed the garden of the bad

actors.

Try to identify drugs that based on the

evidence we have, appear to be less risk in the

totality of their evidence, looking for consistency

study to study to study, and then, in a rational

way, suggest these are the drugs we think that the

public should use, and these other drugs, well,

then you have to decide do you want them on the

market or not.

I am not really going to comment on that,

but I think that is the approach I would take. I

would be trying to sort of identify right off the

bat the bad actors and let's get rid of them.

Things that look like they may actually be

safe, and when I say "safe" now, I mean that they

don't appear to have cardiovascular risk, identify

them and shift the market towards that, and then

deal with the others.

DR. WOOD: Dr. Friedman.

DR. FRIEDMAN: Thank you. Several

comments. First, as both Dr. Graham and Dr. Platt

have mentioned, observational studies are

essential, but they have a number of limitations,

and because of those limitations, it is easy after

the fact to critique away those whose results you

don't much care for as we have seen.

But a couple of other points. One, can

these particular drugs, their primary use, we are

dealing with chronic conditions, conditions that

last years, sometimes many years, and so the drugs

are intended for use over those many years

potentially.

Yet, most of the clinical trials we heard

reported yesterday are 12, 18 weeks, a few of them

go longer. You mentioned that one of the reasons

we didn't see the problems early on may be numbers,

and I agree that is potentially it, but the fact is

we didn't see problems arise in the studies until

14, 18 months.

We often see analyses by patient years of

exposure. In this particular setting, I don't know

whether patient years are always equal to patient

years, and therefore, I guess I would say why

aren't we doing more bigger, longer randomized

clinical trials for these chronic conditions?

DR. GRAHAM: I am not speaking for the

agency now.

DR. WOOD: We got that. Don't say it each

time.

DR. GRAHAM: Okay. I think they are

incredibly expensive and companies don't want to do

them. There is not an incentive for them to do

them, and you would have to talk to the people from

the new drug side of the house, but the fact is

that they are not requiring them.

So, that is a very legitimate question.

You know, working as an epidemiologist, we try to

make do with what is, and so we use the

observational data. You are going to get better

quality data if you are able to do this, but just

to give you a sense of the size of the studies that

I think you would need to do, I mean you talked

about before that you have the APPROVe study and we

see no effect until 18 months, but there was study

090 that was talked about briefly by Dr. Villalba

yesterday. It was a 6-week study at 12.5 mg, and

it showed a difference, the suggestion of a

cardiovascular risk within the 6-week study at the

lowest dose. Now, it's a small study, as well.

But I am just saying that to say that I

think the epidemiologic data, in my mind at least,

answers the question about when the effect begins.

The question is if you want to have--this is the

philosophy--how much certainty do you need to make

a decision.

Right now, when it comes to efficacy, the

effect, does the drug work, you are looking at the

lower bound of the confidence interval, and you

want to see is that different than 1, because if it

is, then, I will conclude with 95 percent certainty

or greater that the drug actually has an effect.

When it comes to safety, you are doing the

same thing. You are looking at that lower bound.

You want this 95 percent certainty that the drug is

harmful. You are presuming that the drug is safe

rather than let's presume we want to do no harm to

patients.

Let's start off at the beginning assuming

that the drug isn't safe, and we want to have a

certain level of confidence about how bad this drug

could be, and that is still tolerable to us. We

want to cap the risk. It will be a completely

different way of looking at studies for a safety

perspective, one that actually gives a priority to

safety and it maximally protective of patient

safety, just as that high standard for efficacy is

maximally protective of patient safety, because by

keeping drugs off the market that don't work, I am

protecting patients from unsafe drugs, and if I

have pneumonia and I am given a drug that doesn't

work, well, I get a harm from that.

But that's philosophy, and I think it's an

outcropping, it's a development, a natural

extension of the development of clinical trials in

the United States where the focus has always been

on efficacy.

DR. WOOD: Let's try and keep both the

questions and the answers reasonably short,

otherwise, we will be here until after midnight.

DR. GRAHAM: I apologize.

DR. WOOD: That's okay. Let's go on to

Dr. Elashoff.

DR. ELASHOFF: First, I have one comment

and then one question. In terms of confounding,

just because you put a lot of variables in some

model doesn't necessarily mean that you have

adequately removed the confounding effects even of

those variables.

The second has to do with Dr. Graham's

slide 13, the excess population risk. I note that

the Ingenix data has been left out of the bottom

category.

DR. GRAHAM: That's right, because for the

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high dose.

DR. ELASHOFF: Yes, but the negative sign

needs to be on the slide, otherwise, it's a biased

presentation.

DR. GRAHAM: Well enough. I take that

correction. Okay, fair enough.

DR. WOOD: Dr. Bathon.

DR. BATHON: Yes. As we weigh the

risk-benefit ratio of these drugs, one

consideration is that there are subgroups of

patients in which the benefit might outweigh the

risk possibly.

With that in mind, it would be helpful for

us who are not cardiologists or epidemiologists to

be able to put the relative risks that we have been

seeing over the past day or two in context with all

the cardiovascular risk factors that exist.

So, for example, if you were take the

presumed relative risk of rofecoxib of 1.5 to 2.0,

at least at the higher dose, and put it into some

context for us of the 20 to 40 cardiovascular risk

factors that exist in a sort of rank order, where

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would you put the COX-2 drugs?

DR. GRAHAM: For the high dose it would

be probably more significant than smoking or

diabetes or hypertension, maybe more important than

the combination of several of those factors in a

patient. For the lower dose, it is probably more

than hypertension, a little less than diabetes, and

a little less than smoking.

I know, David, you know the cardiovascular

risk factors much better than I do, and so does Dr.

Hennekens, but that would be my ballpark on that.

DR. WOOD: Dr. Abramson.

DR. ABRAMSON: Yes. I want to go back to

the question Dr. Shafer asked about if these

classes of drugs or this group of drugs could be if

there was a hierarchy of risk, and you first

answered that you thought the coxibs were more

risky, but I would challenge you a bit simply on

your own presentation.

I would like you to discuss your data,

because you then went on to talk about how

indomethacin has a risk, Meloxicam has a risk.

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Based on your data, the message that came through

is that there was a dose response risk for

cardiovascular outcomes, that we saw it within the

coxibs, but we also saw it where the data were

available in the non-selective NSAIDs.

There are data that we have seen that

ibuprofen might increase risk. We didn't talk

about the McDonald and Way paper that in

cardiovascular discharge patients, people given

ibuprofen had a higher mortality 2-fold.

So, as the smoke clears, I am not sure

that the simple answer that the coxibs were

different was actually supported by your data, nor

your ultimate explanation. Can you defend that?

DR. GRAHAM: I think you are accurate.

What I was saying was I was referring, I think, to

the underlying COX-2 hypothesis and that it is

clearer, I believe, and, well, maybe it's an

overgeneralization, because we have the n that we

are viewing is so small, that looking at rofecoxib

as sort of the example where we can see very

clearly the dose response at all the levels and its

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progression, and understanding its mechanism of

action, and then seeing similar things with

celecoxib and valdecoxib.

I think what you are saying is fair.

Maybe a better thing to say is, in the end, that

you do need to look at it drug by drug.

What I was saying, though, in that answer

that I gave to Dr. Shafer, I was really talking

more about sort of the COX-2 mechanism and the

coxibs as being, in quotes, "COX-2 selective," but

I think your observation is correct.

DR. ABRAMSON: Add to that, that although

there is a hazard that we don't accomplish a lot by

simply saying the class of NSAIDs may have risk, I

think we have under-appreciated that over the last

10 years.

It is not that different from the

mid-nineties recognizing that there was a class GI

effect of these drugs, and that compared to

placebo, whether it's hypertension or long-term

potential adverse outcomes, this is something that

doctors have to be aware of, even the simple thing

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of checking blood pressures when you put people on

any nonsteroidal drug.

So, I don't know that it is necessarily a

bad outcome to call attention to this class effect

until we get better information on each of these

individual drugs.

DR. WOOD: Dr. Day.

DR. DAY: I have a comment about recall

bias and reverse recall bias. There is a huge

research literature on how memory works both in the

laboratory and in the every-day world, and there

are two phenomena that have been very heavily

studied that I think might be relevant here.

One is called flashbulb memory, and the

idea is when an emotional spectacular event

happens, such as when you first learn that JFK had

been shot, or the Challenger blew up, or the World

Trade Center had been hit, it is as if the old-time

flashbulb from an old-time flash camera went off

and captured all the details, and you remember all

of those details forever afterwards associated with

the event that you might otherwise have just not

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even noticed or forgotten.

So, there is a lot of research on

flashbulb memory that shows many of those details

are indeed correct, but some are notoriously false.

For example, there are accounts of people who

remember a certain even with great emotional

aspects to it, and they remember listening the

world series when so-and-so is pitching and it was

the bottom of the 9th, da-da-da, all these details,

and when you go back and check the evidence of what

was going on, on that day and time, that particular

game was not on.

So, that phenomenon number one, flashbulb

memory, and the second is eyewitness testimony.

How you ask a person a question will affect what

answers you get. So, if you have in the courtroom,

someone who has witnessed a car accident, if the

lawyer asks this witness, "Did you see the broken

glass," then, the witness is more likely to say yes

than if you ask, "Did you see any broken glass,"

because the broken glass presumes that there was

some, and so forth.

So, I take your points seriously about

potential recall bias and reverse recall bias, but

we would have to look at both, whether there is an

106

emotional component or not. Those who have had an

MI, for example, would have that most likely, but

also how the questions are asked in these surveys,

and it is not trivial how you ask people questions

about were you taking any medications or were you

taking medication X, and for how long, and what was

the dosage, and so on.

So, I don't think that these details are

always published with the studies, and I would like

to encourage people who ask people about their

experiences with drugs, take a look at the memory

literature for some of these points.

DR. WOOD: Dr. Gibofsky.

DR. GIBOFSKY: Dr. Graham, I am wondering

if you separated out your populations based on the

indication for which they were taking the drug. I

ask that because we heard yesterday, and it's well

known, that rheumatoid arthritis is itself a risk

factor for cardiovascular disease, and higher doses

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of coxibs, in particular celecoxib, are usually

given to patients with rheumatoid arthritis as

opposed to osteoarthritis.

So, I am wondering if you look at that in

your breakdown.

DR. GRAHAM: Several of the studies that I

reviewed have looked at the indication, but in

automated claims data, it is very difficult to be

sort of be sure does the patient have rheumatoid

arthritis, and there are different algorithms one

could use, but in general, what has been found in

the studies where they have looked at that, that

the prevalence of rheumatoid arthritis in the study

populations has been low, very low, and that its

impact on the results when they adjusted for it

didn't materially affect things.

Now, in the California Medicaid study, one

difference in that study was that our base

population was limited to patients who had

diagnoses of osteoarthritis or rheumatoid

arthritis. Now, these are diagnoses, and so does

that mean that they really had osteoarthritis or

108

rheumatoid arthritis, I don't know, but when we did

try to eliminate in that study at least were the

people who might be using an NSAIDs for a muscle

injury, a short-term complaint as opposed to a

chronic illness.

In none of those does the presence of

rheumatoid arthritis seem to affect things, but

again I think the prevalence is pretty low in all

of these studies.

DR. GIBOFSKY: One quick question for Dr.

Platt, if I might. I need to understand the

concept of survivor bias somewhat in that I think

there is a difference between a patient who is

drug-naive, then put on a drug, and then an event

happens versus a patient who may have seen a drug,

perhaps seen another drug after that, 3 or 4 agents

of the class, and is then switched to another agent

and something happens.

I think we have talked about remote versus

current, but there is also this issue of sequential

effect, and I am wondering how you deal with that

as a survivor, particularly because of the paper we

109

saw a few weeks ago in the Archives suggesting that

discontinuation of an NSAID may itself be a risk

factor for a thrombotic event.

DR. PLATT: Your point is exactly right.

I think that the concern about survivor bias is

that if we think that some people are particularly

susceptible, which is almost certainly the case,

then, if we start the clock after a person has

already been exposed to a drug or to one that has

the same effect, then, it is very much less likely

that those individuals will have a problem.

That may be the explanation, for instance,

for the reason that the literature was so badly

wrong about postmenopausal estrogens and heart

disease, that most of the epi studies started with

prevalent users.

I think the majority of the studies that

we were reviewing here, these were individuals who

are known to have had at least a year of prior

experience without exposure to the nonsteroidals.

Your study in Kaiser I know was an

exception cohort at least with regard to a year of

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prior history, but I am not aware that any studies

have a longer drug-free prior interval than that.

DR. WOOD: Dr. O'Neil, do you want to

comment particularly on this?

DR. O'NEIL: Yes, this is an important

point and a lot of things have been covered in

Richard's and David's presentation, but one thing I

think that is relevant that Richard did not cover,

that is, the value of a randomized trial, is the

ascertainment and follow-up, and knowing the status

of individuals in the sense of who goes off therapy

and how long they stay on therapy.

That is very critical relative to the time

dependency of the risk. It was mentioned, for

example, the use in the observational sense of

recent and remote and current use. Those are all

terms that are nice, but they don't get at the

issue that we are trying to get at with regard to

the clinical trials, and that is essentially when

does time zero start for you.

So, I think the appropriate question to

ask is what is the duration of exposure since your

111

initial exposure to the drug, because I think that

is very relevant to the interpretation of the three

clinical trials that we have, two of which are in

placebo-control populations.

There is a rofecoxib-naproxen control

trial for one years, there is a placebo-control

trial in polyp prevention for three years, and

there is a placebo-control trial in Alzheimer's

disease for four years, and the time dependency

from time zero matters as you have seen in the

plots.

It is relevant to the excess risk

calculation. So, I would ask the committee, as

well as I would ask David, of the observational

studies that you have reported, how many of them

are cohort studies, and how many of them are able

to identify new initial use, and then track

continued use for that individual, so that one

could look at the relationship between the hazard

rates and the hazard ratios that we are identifying

in the randomized trials and match that to the odds

ratios that are being reported in the observational

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studies.

DR. GRAHAM: On one of my initial slides,

you can see what the cohort studies were, and in

some of the nested case control studies, you are

also able to get the time on drug. Actually, in

Wayne Ray's cohort study, most of these cohort

studies include prevalent and incident users, so

they will do what is called a "new user"

subanalysis, which is to try to get to this issue

of when does time zero begin.

We addressed that problem in our study

here by the inception cohort design in our base

population, so that we can identify what time zero

was for the cases.

Now, none of those studies presented data

in the form of a survival analysis, which I think

in the end, that is what Dr. O'Neil would like to

see.

DR. O'NEIL: No, my question is not so

much in survival. I don't believe, and again that

is why I am asking you, I don't think any of those

studies were designed or able to capture the

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question I am asking.

In fact, if I am not mistaken, in the

Wayne Ray study, he defined new use, but he did not

define any time from new use, which is essentially

critical to when those risks start.

DR. GRAHAM: That study isn't cited as one

of the studies where we are able to derive that

information. This slide was a slide that I

presented to show that from the epidemiologic

literature, those studies where the investigators

had identified when time zero began for rofecoxib

use, and they didn't present the data as a survival

analysis, but they identified when time zero began

and then, in various ways, showed you either what

the distribution of the cases were, so that you can

see that it was impossible for the risk to have

been delayed for 18 months, because nobody in the

study used the drug for 18 months, or they parsed

time out and looked at the first 30 days of use

from time zero, and found the risks that they found

down here.

But you are right, those studies aren't

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designed that way, and we haven't had time in our

Medicaid study to do these analyses yet, but we

have the data to now do the cohort study and time

to event, so we will have an opportunity actually

within the data to actually compare and look to see

exactly the question you are driving at.

But I would say that from the published

data, in each of these studies, time zero for

rofecoxib was identified and in some way or

another, information that I think could be useful

to the committee in establishing when does risk

begin was contained in those studies.

DR. O'NEIL: Well, the other point here,

which is the value of clinical trials, and it was

the question that was discussed yesterday with

regard to the intent-to-treat analysis, and that is

to say to analyze all outcomes once randomized to

the trial regardless of whether you want to track

the individual to 14 days post-exposure.

You can't really maybe get access to this

information in the observational studies. That is

a conjecture, but it's one or the other biases, and

115

it was interesting to the comment, whether one

would believe this or not, that discontinuation,

discontinuation from an NSAID alone raises risk.

If that were to be the case, that is a

different analysis altogether.

DR. GRAHAM: In that actual paper, it

could be that people were discontinuing the NSAIDs

because they were having chest pain and it was

being interpreted as dyspepsia or something, and

then they go to have their infarct.

I mean you are right about that, but this

is the nature of how epidemiology is done, and I

can't change it. I didn't make the rules, I am

only following them. Nobody is arguing that

clinical trials, if they could be large enough,

that they would give all of us answers that we

would have greater comfort trusting what they are

saying.

What I am proposing is that we don't have

that kind of data in the clinical trials. As large

as the clinical trials are, for the questions that

this committee is facing, you don't have the data

116

you need, and what I presented is the epidemiologic

data, and it is imperfect and it has its warts, and

that is why I would emphasize looking at

consistency and trying to sort of derive from that

a general sense.

I mean does it make pharmacologic sense

that you would have an 18-month delay? I mean I

guess I suppose it depends on what you think the

mechanism of action is for the underlying disease,

but even in the clinical trials, study 090 was 6

weeks long, 12.5 mg, and it had a cardiovascular

effect.

DR. WOOD: I am happy to facilitate a

discussion among the FDA, but I think we would

rather hear from the committee right now. Dr.

Farrar, you are next.

DR. FARRAR: I think that the

recommendations of the committee tomorrow are going

to depend on the assessment of the overall risk and

the overall benefit of this class of drugs.

As a researcher and after all the data

that has been presented, I am more than happy to

117

accept the fact that there are serious risks even

of death from taking NSAIDs. In fact, though,

there are serious risks in taking any medication at

all.

For some of the NSAIDs, it is

cardiovascular risks, for some of them it is

clearly GI bleeding. As a doctor, though, who

takes care of patients, I know that treating pain

or not treating pain and not treating the

disability of arthritis also has very serious risks

even of death.

Given the extensive work that you have

done, on the risk of both the cardiovascular and

the GI bleed, I wonder what level of risk is

acceptable you, and remembering that the only other

drugs that are really available is analgesics or

narcotics, and the only other drugs that are really

available in terms of limiting inflammation are

biologics or immunosuppressants, I wonder what drug

is safe enough that you would recommend that I

actually would be able to use it in patients to

prevent some of their suffering.

DR. GRAHAM: Well, I am not going to give

a product endorsement. A couple of things, though.

DR. WOOD: Try and make it brief.

118

DR. GRAHAM: One, the benefits of the

treatment for the traditional NSAIDs compared to

the COX-2 selective NSAIDs with GI bleed, we have

clinical trial evidence that suggest that there may

be a difference, but here, to me, is an anomaly.

Rofecoxib got the indication for being

GI-protective, celecoxib didn't based on the

clinical trials data you guys looked at yesterday.

There are two published studies in the

literature looking at what I would say is actual

benefit. There, they were looking at

hospitalization for GI bleed--they didn't look at

death from GI bleed, but I wish they had--but

hospitalization for GI bleed, and what they found

was, in both of these studies, that celecoxib was

actually more beneficial, you know, lower rate of

hospitalization for GI than rofecoxib. So, that is

the population, two large studies.

You have got your clinical trials that

119

would have said it should be the reverse. So, I

throw that out as one sort of conundrum.

The second is that I don't think that the

actual benefits of these drugs are understood well

enough to sort of try to weigh these very well.

The case fatality rate for myocardial infarction in

the United States approaches 40 percent. The case

fatality rate for hospitalized GI bleeding is

probably somewhere around 5 or 10, it is a much

lower case fatality rate.

Nobody that I have seen anywhere has sort

of worked this out very well, so I would submit to

you and to the committee that you actually know

very little about the actual population benefit of

any of these products.

DR. WOOD: I don't think we are going to

get an answer to that question, so let's move on.

Dr. Nissen.

DR. NISSEN: Let me briefly answer the

earlier question about what does the hazard ratio

of 1.5 to 2 mean. Before I came to the meeting, I

made a point to look this up, because I thought it

120

would be very relevant.

It is equivalent to raising a cholesterol

from 200 to 260, or taking up smoking. Another way

for the committee, I mean as a cardiologist I have

to deal with this all the time, the most effective

drugs we have for prevention of morbidity and

mortality are statins, and they reduce risk about

35 percent.

So, a hazard ratio of 1.5 to 2 is really a

very, very big effect when you are talking about

the most common cause of mortality, and that is why

this discussion is so important.

Now, my question is this. We are going to

be asked to balance risk and benefit, and so the

magnitude of the hazard ratio is very important to

all of us, and I am trying to reconcile what we see

in the randomized control trials with, let's take

rofecoxib for a moment, where it looks like the

hazard ratio in the randomized trials is in the

range of 2, 3, 4, maybe even higher, and in the

observational data it is significantly lower.

I would like to propose a hypothesis to

121

you and just ask you if you think this is right.

In your observational data, you are looking at

mostly short-term exposure, so you are looking at

less than 12 months typically of exposure.

It may well be that the hazard increases

over time, so that by the time you get to 18

months, you can actually see it in a much smaller

randomized trial, and so it doesn't rule out the

possibility that, in fact, both observations are

right, that, in fact, there is an early hazard, but

that early hazard has a smaller hazard ratio than

the hazard at 18 months or 24 months or even 36

months, and if we ever were to look out 5 years, it

might still be increasing.

Do you think that is a reasonable

hypothesis?

DR. GRAHAM: I think more likely it is,

that in your clinical trials, early on you don't

have enough power to distinguish the risk. The

hazard is the same, but the lines are closer

together, because we are closer to the origin.

I think one other explanation for the

122

lower risk ratios in observational studies, I would

think is more likely due to misclassification of

exposure and misclassification of outcome. It is

likely to be nondifferential, so it would tend to

reduce the odds ratios and relative risks towards

Exposure, because people are going to take

it, a lot of these people are taking it on a prn

kind of basis. In a clinical trial, you have a

greater certitude that they are actually taking it

every day. That introduces a lot of

misclassification, so the a priori hypothesis going

into an observational study, with misclassification

going on, you are fighting an uphill battle to see

an effect.

DR. WOOD: We have got lots of people who

want to ask questions. I want to make sure that

the people who are asking questions have questions

they want to ask for clarification of the speakers

who have spoken rather than just general points.

Dr. D'Agostino.

DR. D'AGOSTINO: I have a couple of

123

questions along the way here. I have spent a good

part of my career in the Framingham Heart Study,

and it's an epidemiological study and a cohort

study, and we take joy when somebody runs a

controlled trial on hypotheses and then later on

confirms it.

The first question is I am concerned that

even though you have gone through this careful

analysis, your conclusions are no apparent effect,

probably increased effect, probable increased risk.

They really don't help us in the sense of pinning

things down. We have a couple of very strong I

think good studies, the APPROVe study and the APC

study as placebo-controlled trials.

Tell us quickly where is the weight of how

we should look at these two pieces, the controlled

trials we have versus what you have produced.

DR. WOOD: Really quickly.

DR. D'AGOSTINO: Really quickly, it can be

done quickly.

DR. GRAHAM: My belief is that for the

controlled clinical trials, for the levels of risk

124

that we are concerned about, that they do not have

the statistical power early on to show risk

differences.

DR. D'AGOSTINO: I think Bob O'Neil's

comment is very important here.

The other two points, and again I will

make them quick, I am very concerned about the high

dose effect you have, and I am really concerned

about the MI and the number of cases. I mean blood

pressure, cholesterol, diabetes, smoking, this is

what drives people to have heart attacks and what

have you, and that is completely missing on your

assessment of how many new cases, so I guess it is

more of a comment that I am really concerned that

that sheet needs sobering interpretation.

DR. GRAHAM: But it was based on the odds

ratios and relative risks where those factors were

adjusted for, so as well as they are adjusted for,

that is what the projection represents, the excess

after adjustment.

DR. D'AGOSTINO: Yes, but I mean the

comment was made by you, throwing in the analysis

125

doesn't necessarily adjust for them.

The last one, you made a very nice point

about the cardio-protective effect, and you tried

to show that these uses, and what have you, somehow

or other all have the same risk, and your

interpretation that there must be some confounding

going on, why doesn't that hold for all the studies

you gave, why don't that hold for the Solomon

study, which you thought was a great study, yet,

this one result you don't like?

DR. GRAHAM: For what, the Kimmel study?

DR. D'AGOSTINO: Wasn't it the Solomon

study that had the naproxen as the

cardio-protective?

DR. GRAHAM: That is because the cardio

protection was present when they were on the drug

and when they weren't on the drug.

DR. D'AGOSTINO: I understand what you are

saying, but if that's a problem, then, it means

there is some confounding going on.

DR. GRAHAM: No, it's selection bias.

DR. D'AGOSTINO: Well, it's selection

126

bias, but why isn't it for the whole study? Why do

you throw out a result you don't like and keep all

the results you like?

DR. GRAHAM: No, that is not what I did.

I pointed out a result where they showed the

presence of the selection bias. In other studies,

the Ingenix study is the only other study that

looked at this. I don't have a slide of it.

DR. D'AGOSTINO: I don't know if it's a

selection bias or misinterpretation of the data.

DR. GRAHAM: Well, to me it looks like

selection bias.

DR. WOOD: Let's continue that

conversation later.

Dr. Morris.

DR. MORRIS: David, would you go to slide

14. That is the risk, the duration of use. I

think one of your points was that if you look at

your study, tell me if I understand this right,

that with the lower dose, that the median time to

an AMI is sooner than with a higher dose, did I

understand that right?

DR. GRAHAM: Yes.

DR. MORRIS: A month?

DR. GRAHAM: Had more cases, a greater

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proportion of our cases, but the other thing is

remember, down here, we are talking about 18 cases

or so. The N here is small, the N here is like 58,

and the N here is 10. So, I wouldn't read too much

into the difference.

The more important point is that at the

low dose, nobody was out there beyond 18 months, so

all the action happened before 18 months, and the

same for the others. I see what you are saying. I

can only say that is what our data were.

DR. MORRIS: One interpretation is what

you said earlier, that for this particular drug, we

are talking about, as you said, no safe level. I

was wondering if that is the way you interpreted

it, that because we are talking about Vioxx here,

and there is no safe level, that something is going

to happen sooner, or is it something with the

populations are different.

DR. GRAHAM: The populations could be

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different, but I think, you know, you would expect

the higher dose to have a shorter latency to onset

than the higher dose, but the numbers are so small.

DR. MORRIS: Okay, it's a small number

problem.

DR. WOOD: So, the answer is too small

numbers at high dose.

Dr. Boulware.

DR. BOULWARE: I just want to make sure I

understand something that you had proposed in your

excess population risk slide, if you would put that

back up.

As a rheumatologist, I use these drugs in

a population much greater than what you have here

with a 65 to 74 where the risk of an MI is fairly

high in that group.

Did you want us to believe that this

excess risk that you are proposing would be

extrapolated to other population groups, too?

DR. GRAHAM: Well, no.

DR. BOULWARE: Do you have any numbers

that may demonstrate that?

DR. GRAHAM: Well, the answer to the

second is no. This was an example in conversation

with people planning the talk, to try to help

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people connect with what it means.

Cardiovascular risks go up. I mean in the

next age group higher, the risks are higher. In

the age groups lower, they are lower, but

cardiovascular risk begins to increase in the 40s.

DR. BOULWARE: I understand, but it

wouldn't be a linear type of thing.

DR. GRAHAM: No, the background risk isn't

linear, the relative risks, though, are adjusted

out.

DR. BOULWARE: Because one of the

questions we will be faced with is are there

subpopulations or groups that these may be safe in,

and I just want to make sure I understand the

relative risk in different age groups.

DR. GRAHAM: Nobody in any of the studies

where they have looked at it have reported effect

modification, which would be that the level of risk

differs at different ages.

DR. BOULWARE: One more question here. I

want to make sure I understand. I think I heard a

comment that says when the risk approaches

2.0--maybe I just assumed that you said this--that

it was an unacceptable level of risk.

Is there ever a case where a drug may have

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a clinical benefit in which that risk is

acceptable, because for the patients I see, not

giving them any of these drugs will confer a great

deal of risk on them, and physical impairment, and

we have studies that show that the functional

classification of rheumatoid arthritis patients

carries with it a significant mortality as that

class goes up?

DR. WOOD: I think that is a question for

the committee to answer rather than Dr. Graham.

Let's move on to Dr. Cryer. Do you have a

question?

DR. CRYER: I do. The comment and

question I have of Dr. Graham addresses an issue

that I think is an important difference between the

observational studies and the prospective studies,

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and this difference relates to assessment of drug

compliance and missed doses, and I think it is

critical as it relates to assessing drugs which

potentially affect platelet function.

A huge difference, as you know, between

aspirin's effect and every other NSAID including

the COX-2 inhibitors, is that with the non-aspirin

NSAIDs, as soon as you remove the drugs, whatever

potential effect they would have had on the

platelet are immediately reversed.

So, with naproxen specifically, my

preconceived bias, which may be wrong, but my

preconceived bias based upon everything I know

about the pharmacology and the things that Dr.

FitzGerald has reviewed for us, is that it should

have some mild anti-platelet effects which would

only be present when the drug is on board in the

system.

So, the specific question is, in the

observational studies, recognizing that in clinical

practice people miss doses of their NSAIDs, they

are not taking their NSAIDs consistently, how do

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you account for the missed doses in the

observational studies recognizing that this could

potentially lead to a mitigation of whatever

negative effect or positive effect that they may

have?

DR. GRAHAM: It ends up being

misclassification. Generally, what that means is it

will force the observed level of risk, the relative

risk of the odds ratio closer to 1. So, if we had

an increased risk, it would make it lower, if we

had a protective effect, it would sort of make it

higher, closer to 1.

DR. CRYER: Right, we agree on that. The

specific question is, is there a way to actually

recognize or to account for when people do not take

their doses in the observational databases?

DR. GRAHAM: No, there isn't, so when you

are studying, say, an increased risk, that is why I

said if you find something, you have to realize you

found it despite the misclassification.

DR. WOOD: Okay. Dr. Domanski.

DR. DOMANSKI: I will save it for

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tomorrow.

DR. WOOD: Okay, great. Dr. Furberg.

DR. FURBERG: No.

DR. WOOD: Okay, great.

Dr. Temple, who does speak for the FDA.

DR. TEMPLE: I am just asking questions.

A couple. Actually, one point is it seems to me

that since we expect that people are going to be

getting one drug or another, comparisons with other

NSAIDs seems like as good a comparison as we should

make. You might want to leave out indomethacin if

you are worried about it. That's one thing.

I guess my main question, though, is

everybody has paid appropriate lip service to the

idea that very small differences are hard to

interpret in epidemiology.

People have said 1.5, 2. Actually, I

notice in one of his editorials, Dr. Furberg cited

a paper of mine where I said anything less than 2

really needs a lot of questions. Jerry Cornfield,

who sort of invented all this stuff, used to say 3.

Well, we are talking about differences

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here that are 0.1 differences, not that they

wouldn't be hugely important if they were true,

that is absolutely true. So, I guess I want to

know what Richard and you make of all this, because

the numbers are very small, and yet, just as an

example, there is a very great consistency that you

cite that celecoxib looks sort of okay, but you

found one study where there is a little hint that

maybe the higher dose is a problem, and since

probably we all think dose response is likely, that

looks good to you.

DR. GRAHAM: Two studies, there were 2.

DR. TEMPLE: Okay, 2. The valdecoxib

data, which shows nothing, doesn't look so good

because we probably all believe that there is

likely to be a class effect.

What I am asking is, with numbers like

this, how do you know what to do with them? That

seems very fundamental for the epidemiology.

DR. WOOD: But, Bob, there are 4

randomized clinical trials here, and your comments

don't apply to them, I assume.

DR. TEMPLE: No, they don't, although they

are not perfectly consistent either. But, no, I am

asking, what do we make of differences of this

135

magnitude with everybody having given lip service

to the idea that small differences are hard to

interpret, and yet we seem to be enthusiastically

endorsing them, so I just want to know what Richard

and David think about that.

DR. GRAHAM: Rich, do you want to go

first?

DR. PLATT: I think we have to be cautious

about how we interpret it, so I would say the

finding of a relative risk of 3 in an epidemiologic

study, as David found, is meaningful--

DR. TEMPLE: For high dose rofecoxib.

DR. PLATT: For high dose rofecoxib.

DR. TEMPLE: I would not dispute that at

all.

DR. PLATT: It seems to me that in that

context, that a dose response effect, that the

information about lower doses gains weight by

borrowing from that. I think that is also worth

136

keeping in mind when, in other studies that are

working in that range that make us all nervous,

there appears to be a dose response effect.

It is the kind of consistency that makes

the study, in my mind, be worth more attention. I

think there is something to be said for giving more

weight to relatively small excess risks if they are

seen in a number of different environments when we

can't have good reason to think that there is a

similar kind of biases that might be contributing

to it.

After that, I agree with you. We are in

relatively difficult terrain. I think that it is

not the same as no data, though. I think we ought

to distinguish between the situation in which we

have no evidence from ones in which we have

relatively weak evidence.

We didn't talk at all, for instance, about

the enormous number of spontaneous reports of

myocardial infarction following exposure to

nonsteroidals. There are thousands and thousands

of them. In my mind, they don't contribute at all

137

to the discussion, whereas, I think these need to

be weighed in the mix when we don't have clinical

trial information to depend on.

DR. GRAHAM: My answer is similar to his,

but I think that what you are identifying is, is

that we are hitting or at least right now the

frontier is the limits of what the available tools

we have to define the levels of risk that we are

talking about.

We are talking about small levels of risk

that turn out for this particular event to be

enormously important in a population level. If you

are talking liver failure, we wouldn't be having

this conversation. For that reason, it becomes

important and what I would say is sort of

emphasizing what Rich said, is I would be looking

for consistency across different studies, and if I

found a number of studies, say, as with Indocin,

for example, to me, that is more persuasive.

If I found a number of studies that

pointed to a particular set of NSAIDs that seems to

have low risks, I would take comfort in that in the

138

absence of perfect information. I mean some light

in a storm is probably better than no light In a

storm.

DR. TEMPLE: I take it if the differences

were at the level of 10 percent, 1.1 versus 1.2--

DR. GRAHAM: I am thinking more in a very

qualitative sense of things that they seem to

cluster around 1. I mean 1.1 for ibuprofen, it

could be that, for example, may naproxen increases

the risk 3 percent in the real world, we are never

going to figure that out, maybe ibuprofen increases

it 10 percent or 15 percent, maybe we could figure

that out, I don't know, but there is going to be a

place where qualitatively, if we see enough studies

kind of sort of pointing to the same place, you

know, most of them, they are not all going to say

the same thing, there is going to be these

conflicts, just like we have in clinical trials

data.

But if most of the compass arrows are sort

of pointing in the same direction for particular

NSAIDs, I think those are the ones that at least

139

that I sort of place on a suspect list.

DR. TEMPLE: So, very low hazards need at

least multiple support before they are credible.

DR. GRAHAM: I think so, and I think that

you want to try to encourage to collect that

information sort of to test that out.

DR. TEMPLE: Alastair, could I take half a

second to answer a question Larry raised before?

DR. WOOD: Sure, a second.

DR. TEMPLE: Well, it's a very good

question, you know, if the drug is going to be used

forever, why don't you study them forever. The

only thing I would point out here is that what sort

of started people thinking was VIGOR, and VIGOR

didn't take 3 years to show anything, it showed up

in 9 months.

So, what you have seen is for, say,

lumiracoxib, a humongous study of about the same

length, but, of course, they didn't know about

APPROVe, did they, and whatever you think APPROVe

means, whether Bob is right that it's late, or

David is right that there weren't enough cases,

140

people were pointing toward a study that by every

reasonable thought, if you think platelets are

involved, ought to be long enough to show things

up.

But then you form a new hypothesis once

you have APPROVe, and you have to adapt it, and I

think that goes on all the time. It would not be I

must say for most things my first thought unless

you are looking for cancer that you need a 3-year

study to find it, but maybe you learned that it

does.

Just for what is worth as an example, you

can't get an anti-arrhythmic drug approved in this

country without showing that you don't alter

survival unfavorably. One result is there are

hardly any being developed, but, you know, we had

bad experiences, we didn't like the results of

CAST, so you change.

I think there is no doubt that things

evolve and you have to expect that, and APPROVe,

depending on what you think of it, changes the

nature of what you expect.

DR. GRAHAM: Bob, just one point on that.

I think if the APPROVe study had been 5 or 10 times

larger than it was--I am talking about retrospect

141

now--you would be able to answer with much greater

confidence what is happening month 1 to 18. I

guess what I am saying is that you could also

shorten the latency to identification of a problem

if it turns out that the risk is early on.

DR. TEMPLE: David, I think that is

entirely possible, and if it involves platelets, I

would believe you, but if it involves a small,

long-term increase in blood pressure, then, I am

not so sure.

DR. GRAHAM: Right, but we saw yesterday--

DR. TEMPLE: We don't know.

DR. GRAHAM: We don't, but if it's

prostacyclin, that effect could occur immediately.

DR. TEMPLE: Yes, but the blood pressure

effect could be delayed.

DR. WOOD: Right. So what, Bob, you are

saying is that it is easy to be a Monday morning

quarterback, but the data were not there before.

DR. TEMPLE: I would never be that rude.

DR. WOOD: I think you are right.

Dr. Stemhagen.

DR. STEMHAGEN: I would like to clarify a

couple things. First, I am a little concerned in

terms of the unpublished data. I appreciate that

142

we are able to get data very quickly, right at the

minute that it is being generated, but none of us

have had a chance to really review that, so I do

have some concerns about the weight putting on this

unpublished data when the rest of us haven't had a

chance to look at it.

I think there needs to be some

clarification. There was some discussion about the

recall bias, and so on. Certainly, there is a major

concern about that in case- controlled studies, and

we don't have the questionnaires, but there were a

lot of sort of subanalysis done in the Kimmel

study, about trying to look at whether recall bias

is a problem, and I am not sure that you have

highlighted that enough that looking at all those

different things, there were really no differences

143

found.

Similarly, in the Watson study, it's a

GPRD study, it is different than a lot of the large

databases, the automated databases.

There is a lot more personal involvement

in terms of the data and the data collection and

the adjudication of results, and I think it just

needs to be clear that all of these studies are not

the same in terms of a Medicare study where we

can't go back and validate records. A lot of them

had a much more careful review, and I am just not

sure that that was totally clear and if you hadn't

read each of the papers.

I would like to just ask a question in

terms of your definition of the inception cohort,