[Federal Register Volume 61, Number 233 (Tuesday, December 3, 1996)]
[Notices]
[Pages 64099-64136]
From the Federal Register Online via the Government Publishing Office [www.gpo.gov]
[FR Doc No: 96-30648]
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DEPARTMENT OF HEALTH AND HUMAN SERVICES
[Docket No. 84N-0168]
Cyclospasmol; Final Decision on Proposed Withdrawal of
Approval of New Drug Application
AGENCY: Food and Drug Administration, HHS.
ACTION: Notice.
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[[Page 64100]]
SUMMARY: The Food and Drug Administration (FDA) is announcing that the
Commissioner of Food and Drugs (the Commissioner) is issuing his Final
Decision on the proposal to withdraw approval of the new drug
application (NDA) for the human drug product Cyclospasmol
(cyclandelate) (NDA 11-544). This drug is labeled for use in two
indications: specifically, as a treatment for intermittent claudication
caused by arteriosclerosis obliterans and as a treatment for cognitive
dysfunction in patients suffering from senile dementia of the
multiinfarct or Alzheimer's type. The Commissioner has determined that
Cyclospasmol has not been shown to be effective for such
uses, and the Commissioner hereby withdraws approval for this drug. The
Commissioner's Decision sustains the Initial Decision of the
Administrative Law Judge (ALJ), who found that Cyclospasmol
had not been shown by sufficient evidence of adequate and well-
controlled studies to be effective for its intended uses.
EFFECTIVE DATE: January 2, 1997.
ADDRESSES: The transcript of the hearing, evidence submitted, and all
other documents cited in this decision may be seen in the Dockets
Management Branch (HFA-305), Food and Drug Administration, 12420
Parklawn Drive, rm. 1-23, Rockville, MD 20857, from 9 a.m. to 4 p.m.,
Monday through Friday.
FOR FURTHER INFORMATION CONTACT: Nancy E. Pirt, Office of Health
Affairs (HFY-1), Food and Drug Administration, 5600 Fishers Lane,
Rockville, MD 20857, 301-443-1382.
SUPPLEMENTARY INFORMATION: The purpose of this proceeding has been to
determine whether FDA should withdraw approval of the NDA for the human
drug product Cyclospasmol (cyclandelate). This drug is being
offered for use in two indications, specifically: (1) As a treatment
for intermittent claudication caused by arteriosclerosis obliterans
(AHP Exceptions at 14; AHP Post-Hearing Brief at (1), and (2) as a
treatment for cognitive dysfunction in patients suffering from senile
dementia of the multiinfarct or Alzheimer's type. (AHP Exceptions at
111; AHP Post-Hearing Brief at 1.)
Under Sec. 12.130 (21 CFR 12.130), the Commissioner makes the
following decision adjudicating the significant issues raised by the
parties following the administrative hearing. The effect of this
decision is that this drug may no longer be marketed in the United
States.
Because the Commissioner's discussion of the issues is necessarily
detailed, an outline of this discussion is being given for the reader's
convenience:
I. The Commissioner's Final Decision
A. Background
B. The Legal Standard
C. The Intermittent Claudication Indication
1. The MDS-96 (Reich) Study
a. Objective of the Study
b. Test for Presence of Disease
c. Foot Pedal Ergometer as an Evaluative Measure
d. The Winsor Study
e. Adequacy of the MDS-96 (Reich) Study
2. The Five-Center Study
a. Reanalysis of the Five-Center Study
b. Inclusion/Exclusion Decisions
c. Calculation of Treadmill Distances
d. Variability Among Centers
e. Adequacy of the Five-Center Study
D. The Senile Dementia Disease Indication
1. The Rao Study
a. Admissibility of the Reanalysis
b. Labeling and Patient Selection
c. Concomitant Diseases and Conditions
d. Concomitant Medications
e. Case Report Forms
f. Blinding and Bias
g. Adequacy of the Rao Study
2. The Yesavage Study
a. Selection of Patients for the Study
b. Distribution of Patients with Strokes
c. Baseline Comparability
d. Concomitant Medications
e. Small Sample Size
f. Clinical Significance
g. Multiple Tests
h. Adequacy of the Yesavage Study
II. Conclusion and Order
I. The Commissioner's Final Decision
A. Background
Cyclospasmol is a drug consisting of 200 milligrams (mg)
of cyclandelate. (G-33.2 at 7.) 1 The NDA for
Cyclospasmol (NDA 11-544) was approved at a time when the
Federal Food, Drug, and Cosmetic Act (21 U.S.C. 301 et. seq.) (the act)
required only proof of safety. In 1962, the act was amended by the Drug
Amendments Act of 1962 (Pub. L. 87-781) to provide that drugs could no
longer be approved unless both safety and efficacy had been proved.
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\1\ The Dockets Management Branch used the letter ``G'' to refer
to the Government exhibits by the participants.
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The act, as amended, also required FDA to evaluate drugs approved
before 1962 to determine whether such drugs were effective and to
withdraw approval for any NDA where ``substantial evidence'' of the
drug's effectiveness was lacking. (Section 505(e)(3) of the act (21
U.S.C. 355(e)(3)).) FDA's review of these pre-1962 drugs for
effectiveness is known as the Drug Efficacy Study Implementation (DESI)
program. The act placed the burden of coming forward with evidence of
effectiveness on the manufacturer of the drug. (Weinberger v. Hynson,
Westcott and Dunning, 412 U.S. 609, 617 (1973), citing 21 U.S.C.
355(e)(3).)
The Commissioner announced in a notice published in the Federal
Register of July 20, 1971 (36 FR 13347), that he had evaluated a report
received from the National Academy of Sciences/National Research
Council (NAS/NRC) Drug Efficacy Study Group pertaining to certain
peripheral vasodilators for oral use, including Cyclospasmol
Capsules and Tablets. Under the NAS/NRC report, the Commissioner
classified Cyclospasmol as possibly effective for its labeled
indications, except for those claims specifically found in the notice
to lack substantial evidence of effectiveness.
In a notice published in the Federal Register of December 14, 1972
(37 FR 26623), the FDA announced that it would permit
Cyclospasmol capsules and tablets, as well as other
peripheral vasodilators, to remain on the market beyond the time limits
prescribed for implementation of the DESI program. In a subsequent
notice published in the Federal Register of July 11, 1973 (38 FR
18477), FDA required that by September 10, 1973, persons interested in
conducting clinical studies to determine the effectiveness of
peripheral vasodilators to submit protocols and provide the agency with
notice of the date when such studies were expected to begin.
On June 20, 1978, the manufacturer of Cyclospasmol, Ives
Laboratories, a wholly owned subsidiary of American Home Products
(hereinafter referred to as ``AHP''), submitted to FDA's Bureau of
Drugs (currently the Center for Drug Evaluation and Research
(hereinafter referred to as ``the Center''), a status report of five
completed studies for peripheral vascular disease and five completed
studies for cerebral vascular disease studies. These studies were
reviewed by the Center and found not to provide substantial evidence of
adequate and well-controlled studies indicating the effectiveness of
Cyclospasmol for its labeled indications. In two subsequent
notices published in the Federal Register of May 25, 1979 (44 FR 30436;
44 FR 30443), FDA proposed to withdraw approval for
Cyclospasmol's NDA and offered an opportunity for a hearing
on the proposed withdrawal. Ives Laboratories (hereinafter referred to
as ``AHP'') was also given until May 26, 1980, to complete any studies
which were still in progress.
On June 25, 1979, AHP filed a request for a hearing, and this
request was granted by the Commissioner on October 18, 1984 (49 FR
40972). Under
[[Page 64101]]
21 CFR 12.45, both the Center and AHP filed notices of participation. A
prehearing conference was held on January 15, 1985. Following the
submission of written testimony and documentary evidence, a hearing was
held before ALJ Daniel J. Davidson beginning on June 18, 1985, and
ending on June 27, 1985.
Subsequently, on September 25, 1986, Judge Davidson issued his
decision, in which he found that the efficacy of Cyclospasmol
had not been proved by substantial evidence of adequate and well-
controlled clinical trials, and concluded that the approval of NDA 11-
544 should be withdrawn. Both AHP and the Center filed exceptions to
various points in Judge Davidson's decision and appealed to the
Commissioner, under 21 CFR 12.125.
B. The Legal Standard
I am issuing this Final Decision under Sec. 12.130. In taking this
action, I have all the powers I would have had in making the Initial
Decision. (Sec. 12.130(a); see also Commissioner's Decision on
Polychlorinated Biphenyls (49 FR 21514 at 21519, May 22, 1984).)
Further, under Sec. 5.10 (21 CFR 5.10(a)(1)), I have been delegated the
authority by the Secretary of the Department of Health and Human
Services ``to determine, after giving full consideration to all of the
evidence that has been submitted, including expert opinions, if the
(evidence) meet(s) the regulatory criteria and show(s) effectiveness.''
(Warner-Lambert Co. v. Heckler, 787 F.2d 147, 154 (3d Cir. 1986).)
In the present case, I have fully reviewed the complete
administrative record, including: (1) The transcript of the hearing
that was held before the ALJ from June 18, to June 27, 1985; (2) the
written testimony and documentary evidence submitted by AHP and the
Center before, during, and after the Hearing; (3) the exceptions which
AHP and the Center filed to the ALJ's Decision; and (4) all briefs
filed by AHP and the Center pursuant to this matter. My Decision is
based upon a full review of the facts and arguments that appear in the
record, and my independent conclusions are based upon that review.
AHP first argues that the ALJ's decision did not meet the minimum
standard required by the Administrative Procedure Act and by FDA
regulations pertaining to initial decisions following formal
adjudicatory proceedings. (AHP Exceptions at 3, citing 5 U.S.C. 557(c)
and 21 CFR 12.120(b).) In support of its argument, AHP cites the
Administrative Procedure Act for the requirement that all initial
decisions shall include a statement of ``findings and conclusions, and
the reasons or basis therefor, on all the material issues of fact, law,
or discretion presented on the record * * *.'' (AHP Exceptions at 3,
quoting 5 U.S.C. 557(c).) AHP also cites FDA regulations requiring that
initial decisions contain findings of fact based upon relevant,
material and reliable evidence in the record and also contain ``(a)
discussion of the reasons for the findings and conclusions, including a
discussion of the significant contentions made by any participant''
with ``(c)itations to the record supporting the findings and
conclusions * * *.'' (AHP Exceptions at 3, quoting 21 CFR 12.120(b).)
AHP argues that the ALJ did not state how he arrived at his
findings of fact. (AHP Exceptions at 8.) Ignoring the bulk of the ALJ's
decision, AHP refers to the concluding section of the ALJ's decision,
which is appropriately entitled ``Conclusions,'' to argue that the ALJ
simply announced his findings in one sentence decrees. (AHP Exceptions
at 9, citing the ALJ's Initial Decision (I.D.) at 23.)
An identical issue was addressed in the Commissioner's Decision on
Lutrexin, wherein the Commissioner stated:
(The manufacturer) implies that the findings and order are
deficient because the numbered findings of fact at the end of the
narrative do not contain the evidentiary details that (the
manufacturer) feels would justify the judge's ruling. Those details,
however, are fully set out in the judge's narrative explanation.
Stating, discussing, and resolving factual issues in narrative form
rather than in numbered paragraphs is a commonly used format that
has been specifically recognized as fulfilling the Administrative
Procedure Act requirement of a ``statement of * * * findings and
conclusions * * * on all the material issues of fact, law, or
discretion. 5 U.S.C. 557(c). Gilbertville Trucking Co. v. United
States, 196 F. Supp. 351 (D. Mass. 1961); State Corporation Comm. v.
United States, 184 F. Supp. 691 (D. Kan. 1959). ``An agency which
issues opinions in narrative and expository form may continue to do
so without making separate findings of fact and conclusions of
law.'' Attorney General's Memorandum on the Administrative Procedure
Act 86 (1947). So too may an Administrative Law Judge.
(Commissioner's Decision on Lutrexin, 41 FR 14406 at 14410, April 5,
1976.)
I have reviewed the ALJ's decision in the present matter, and I
find that it comports with the previously cited requirements of the
Administrative Procedure Act and FDA regulations. As in the
Commissioner's decision regarding Lutrexin, I find that the ALJ fully
set out the reasons for his decision in the narrative explanation
section of the Initial Decision. Therefore, I find no merit in AHP's
argument.
AHP further argues that the ALJ erred in concluding that at least
two adequate and well-controlled studies are necessary to establish
efficacy. (AHP Exceptions at 2 n.1; I.D. at 8.) As with AHP's previous
objection, this issue, too, has been settled in previous Commissioner's
decisions. In the Commissioner's Decision on Oral Proteolytic Enzymes
(OPE), it was held that, except in certain limited cases, a minimum of
two adequate and well-controlled studies are required. (Commissioner's
Decision on OPE, slip op. at 23, FDA Docket No. 75N-0139 (FDA May 30,
1985), aff'd sub nom. on other grounds Warner-Lambert Co. v. Heckler,
787 F.2d 147 (3d Cir. 1986).) This requirement arises from the
statutory language of the act at 21 U.S.C. 355(d), which mandates the
submission of a plural number of adequate and well-controlled
investigations. (Commissioner's Decision on OPE, slip op. at 23;
Commissioner's Decision on Deprol (58 FR 50929 at 50936, September 29,
1993).)
FDA has permitted exceptions to the requirement for at least two
adequate and well-controlled studies in limited circumstances,
including: (1) When the disease is very rare and it is extremely
difficult to obtain enough subjects for two studies, (2) when the
disease process is expensive to study experimentally, (3) when the
study conducted is very large and multicentered, and (4) when the
disease is rapidly fatal and there is no alternative therapy.
(Commissioner's Decision on OPE, slip op. at 24; Commissioner's
Decision on Deprol, 58 FR 50929 at 50936.) AHP does not argue that any
of these exceptions apply to the present case, nor do I find these
exceptions to be applicable. Therefore, I find no merit in AHP's
objections to the ALJ's ruling that at least two adequate and well-
controlled studies are necessary to demonstrate the efficacy of
Cyclospasmol .
Finally, AHP argues that many sections of the ALJ's Decision
paraphrase, or contain recitations of, portions of the post-hearing
briefs filed by the Center and AHP. AHP states that, as a result,
``(t)he substantive statements made by the ALJ raise questions as to
the ALJ's understanding of the issues.'' (AHP Exceptions at 12.) AHP
has not cited, however, any authority which indicates that it is
impermissible for an ALJ to paraphrase or recite in his decision
statements from the post- hearing briefs. After reviewing the ALJ's
Decision, I find that the ALJ fully set out the reasons for the
conclusions he reached. Additionally, I find that AHP's claim that
``(t)he ALJ's Decision fails to
[[Page 64102]]
meet the requirements of the APA or of FDA's regulations'' (id.)
because the ALJ paraphrased or reproduced language which was submitted
in the post-hearing briefs is without merit.
Moreover, I have fully reviewed the administrative record, and, as
discussed above, have reached independent conclusions from the evidence
presented to the agency and to the ALJ. For the following reasons, I
find that there is a lack of substantial evidence that Cyclospasmol \
will have the effect it purports or is represented to have under the
conditions of use prescribed, recommended, or suggested in its
labeling, and I therefore affirm the Initial Decision of the ALJ.
C. The Intermittent Claudication Indication
The labeling for Cyclospasmol \ previously described its first
indication as being for an ``adjunctive therapy in intermittent
claudication; arteriosclerosis obliterans; thrombophlebitis (to control
associated vasospasm and muscular ischemia); nocturnal leg cramps;
(and) Raynaud's phenomenon.'' (G-33.2 at 7; see also A-89 at 2-4; G-57
at 2-4.) However, AHP has modified this proposed indication to limit it
to treatment of intermittent claudication caused by arteriosclerosis
obliterans. (See AHP Post-Hearing Brief at 1; AHP Exceptions at 14.)
Peripheral vascular disease is a generic name given to diseases
that affect the arteries, veins, and lymphatics in the arms and legs.
(Coffman, G-58 at 1; Vyden, G-59 at 3.) The most common peripheral
vascular disease is arteriosclerosis obliterans, in which a buildup of
cholesterol and fatty acids accumulates in the lining of the arteries
of the legs. This condition results in a narrowing of the lumens of
these vessels, with consequent decreased blood flow to the muscles.
(Coffman, G-58 at 2; Vyden, G-59 at 3.)
The first indication for which Cyclospasmol \ is labeled is as a
treatment for intermittent claudication caused by arteriosclerosis
obliterans. (AHP Exceptions at 14; AHP Post-Hearing Brief at 1.)
Arteriosclerosis obliterans can cause intermittent claudication, which
is pain, cramps, fatigue, or weakness in the legs during exercise.
(Coffman, G-58 at 1-2.) A patient with intermittent claudication
experiences exercise-induced pain in the calf or thigh muscles caused
by a lack of oxygen in the blood being supplied to the leg muscles
after walking a certain distance. (Reich, Tr. Vol. V at 17; Vyden, G-59
at 3.) Typically, pain is relieved within 1 to 3 minutes after resting.
(Reich, Tr. Vol. V at 17; see also Coffman, G-58 at 2 (Dr. Coffman
testified that relief should come within 5 to 10 minutes).) If relief
takes longer to come, then the problem is not likely to be intermittent
claudication. (Reich, Tr. Vol. V at 17.)
AHP submitted two studies--the MDS-96 (Reich) study and the five-
center study--in support of the indication for intermittent
claudication. Each of these studies will be discussed in turn.
1. The MDS-96 (Reich) Study
The MDS-96 study, also referred to as the Reich study, was
conducted by Dr. Theobald Reich as a 12-week, crossover study of 39
patients with arterial insufficiency. The stated purpose of the study
was ``(t)o determine the effect of cyclandelate
(Cyclospasmol), in comparison with a placebo, on the clinical
course and certain vasomotor reflexes in patients with peripheral
vascular disease.'' (G-25.2 at 163.) Each patient was in the study for
12 weeks, assigned to either 6 weeks on the test drug followed by 6
weeks on the placebo, or vice versa. (G-9.1 at 2.) Patients included in
the study were to have a diagnosis of peripheral vascular disease,
including one or more of the following symptoms: Intermittent
claudication, rest pain, cold extremities, or peripheral cyanosis. (G-
25.2 at 163.)
The evaluation of the subjects included skin temperature, skin
color, pulse, distance walked prior to claudication, and severity of
pain at rest. (G-25.2 at 164.) Additionally, skin temperature of the
toes and foot, reactive hyperemia time, blanching time on elevation,
and rubor time on dependence was also to be measured. (G-25.2 at 164.)
The protocol further stated that vasomotor reflexes of the leg and calf
blood flow were to be measured at the beginning of the study and at 2-
week intervals during the study by means of venous occlusion
plethysmography with a mercury-in-rubber strain gauge. (G-25.2 at 164.)
Blood flow was to be measured at rest in the recumbent position, and
after exercise on a foot pedal ergometer. (G-25.2 at 164.)
Exercise on a foot pedal ergometer was performed by a patient in a
supine position, with the patient using his or her foot to repeatedly
raise a weight attached to the foot ergometer pedal. (Reich, A-112 at
29; Denton, A-121 at 3-4.) Exercise on the foot pedal ergometer was to
be continued until claudication or, if pain did not appear, was to be
discontinued after 500 plantar flexions of the foot. (G-25.2 at 164.)
Thirty-nine patients were entered into the study. (Reich, A-112 at
13.) While all 39 patients completed the study, only 32 were found to
be suitable for inclusion in the statistical analysis. (G-9.1 at 252.)
Seven patients were excluded from analysis for failure to take the
required dose during a 2-week interval. (G-9.1 at 252.) The results of
the analysis reported a statistically significant difference in favor
of Cyclospasmol on the mean number of foot pounds of work
that could be performed on the foot pedal ergometer. (Reich, A-110 at
10.)
The ALJ concluded that the Reich study was not an adequate and
well-controlled investigation because: (1) The protocol failed to
clearly identify the condition to be studied, (2) patient selection was
marred by the lack of an objective test to determine the presence of
the disease, and (3) reliance on the foot pedal ergometer to measure
patient improvement in walking ability was not shown to be proper.
(I.D. at 23.)
a. Objective of the study. The ``objective'' section of the Reich
study protocol read in its entirety, ``To determine the effect of
cyclandelate, in comparison with a placebo, on the clinical course and
certain vasomotor reflexes by objective measurement in patients with
peripheral vascular disease.'' (G-25.2 at 163.) The ALJ, after
reviewing the arguments by both AHP and the Center (see I.D. at 12),
ruled, ``Because the objective of the Reich study was to determine the
effect of the drug on certain vasomotor reflexes, it failed to clearly
identify and isolate the condition to be studied.'' (I.D. at 55.) AHP
raises several issues regarding this ruling.
First, AHP argues that the ALJ erred in restricting himself to a
reading of the section of the protocol entitled ``Objective'' when the
ALJ determined the study's objective. (AHP Exceptions at 25.) AHP
argues that under FDA regulations, AHP was not required to have a
separate section in its protocol for the objective, and that it was
acceptable if the objective of a study could be ascertained from a
reading of the complete study protocol. (AHP Exceptions at 26.) AHP
also questions what the ALJ meant by finding that the Reich protocol
``failed to clearly identify the condition to be studied.'' (AHP
Exceptions at 28, quoting I.D. at 23.) AHP further asks how the ALJ
concluded that the sole objective of the Reich study was to determine
the effect of the drug on ``certain vasomotor reflexes.'' (AHP
Exceptions at 28, quoting I.D. at 55.)
The Center counters by arguing that the vagueness of the objective
for the Reich study lies in the absence of a clear statement in the
protocol identifying
[[Page 64103]]
intermittent claudication as the focus of the study. (Center Response
to AHP Exceptions at 7-11.) The Center points to the fact that
intermittent claudication was only one of a number of symptoms in the
patient selection criteria, and that patients were not required to have
intermittent claudication in order to enter the study. (Center Response
to AHP Exceptions at 8.) In sum, the Center is arguing that although
AHP is now submitting the Reich study as proof of
Cyclospasmol's efficacy in treating intermittent
claudication, the Reich study's protocol was vague in identifying this
as the objective of the study. I find the Center's arguments to have
merit.
For a study to be considered adequate and well-controlled, FDA
regulations require the study to contain ``a clear statement of the
objectives of the investigation.'' (Sec. 314.126(b)(1) (21 CFR
314.126(b)(1)); see also Commissioner's Decision on Cothyrobal (42 FR
28602 at 28613, June 3, 1977).) The reason for requiring a clear
statement of objective was aptly summarized by Dr. Marvin Schneiderman,
a statistician and one of the witnesses for the Center, who testified,
``Having a vague objective means that you have a free hand to examine
any kind of data and decide after the fact what data are important to
report in relation to this kind of objective.'' (Schneiderman, G-65 at
5.)
Turning first to that section of the protocol entitled
``Objective,'' I note that the Reich study set out its focus in general
terms as being on ``the clinical course and certain vasomotor reflexes
* * * in patients with peripheral vascular disease.'' (G-25.2 at 163.)
In another section of the protocol, entitled ``Number and Kind of
Subjects,'' the protocol stated that it was anticipated that the
underlying diagnosis for the patients would be ``atherosclerosis of the
arterial vessels of the extremities.'' (G-25.2 at 163.) As described in
this section, patients admitted to the study were required to have
``one or more of the following symptoms: intermittent claudication,
rest pain, cold extremities, or peripheral cyanosis.'' (G-25.2 at 163.)
While AHP is correct in stating that FDA regulations do not require
a section entitled ``objective'' in the protocol, nevertheless, I am
not persuaded by AHP's argument because I find the objective of the
Reich study to be vague even after having read the entire protocol. As
is evident from reading the entire protocol, intermittent claudication
was not a necessary requirement for inclusion in the study. I find that
the protocol does not clearly identify intermittent claudication as the
intended object of the study. A clear statement of objectives is
required by the regulations. (Sec. 314.126(b)(1).) Not finding the
objective to be clear in the protocol, I therefore find no error in the
ALJ's decision on this point.
Next, AHP argues that the ALJ failed to read the ``Objective''
section of the protocol correctly. (AHP Exceptions at 27.) AHP argues
that in the ALJ's opinion, the ALJ incorrectly quoted from the
``Objective'' section of the MDS-96 protocol.
As previously discussed, the ALJ wrote in his opinion that he had
found that the objective of the Reich study was ``to determine the
effect of cyclandelate on certain vasom(otor) reflexes in patients with
peripheral vascular disease as compared to those patients on placebo.''
(I.D. at 12-13.) The verbatim statement of objective in the protocol
read, ``To determine the effect of cyclandelate, in comparison with a
placebo, on the clinical course and certain vasomotor reflexes by
objective measurement in patients with peripheral vascular disease.''
(G-25.2 at 163.) In the ALJ's ruling, the ALJ left out the phrases ``on
the clinical course'' and ``by objective measurement,'' which AHP
argues contributed to the ALJ's assertedly erroneous conclusion
regarding the objective. I find AHP's argument to be without merit.
With or without the phrases in question, the identification of the
study's objective fails because the purpose of the study is not clear
from a reading of the protocol.
AHP also takes exception to the ALJ's decision on the grounds that
the ALJ did not expressly state how much weight he gave to the
testimony of AHP's witnesses who testified in support of the objective
contained in AHP's protocol. (AHP Exceptions at 28.) AHP offers no
legal authority as a basis for asserting that the ALJ must expressly
assign a weight to the testimony of witnesses, and I find this argument
to be without merit. The ALJ is not required to make findings on all
the evidence when the findings he has made support his decision. (See
Immigration and Naturalization Serv. v. Bagamasbad, 429 U.S. 24, 25
(1976); Deep South Broadcasting Co. v. FCC, 278 F.2d 264, 266 (D.C.
Cir. 1960); Community & Johnson Corp. v. United States, 156 F. Supp.
440, 443 (D.N.J. 1957).) If the ALJ identified at least one conclusive
deficiency in each of the studies proffered, the ALJ's decision must be
upheld. (American Cyanamid Co. v. FDA, 606 F.2d 1307, 1314 & n.53 (D.C.
Cir. 1979); SmithKline Corp. v. FDA, 587 F.2d 1107, 1120-21 (D.C. Cir.
1978); Masti-Kure Products, Inc. v. Califano, 587 F.2d 1099, 1104 (D.C.
Cir. 1978); Cooper Laboratories, Inc. v. FDA, 501 F.2d 772, 779-81
(D.C. Cir. 1974).) Also, the ALJ is not required to accept the opinion
of expert witnesses, as such testimony is only as strong as the studies
on which it is based. (Warner-Lambert Co. v. Heckler, 787 F.2d 147, 154
(3d Cir. 1986); Commissioner's Decision on OPE, slip op. at 22, citing
Upjohn Co. v. Finch, 422 F.2d 944 (6th Cir. 1970); Commissioner's
Decision on Deprol, 58 FR 50929 at 50930.) For these reasons, I find no
error in the ALJ's decision on this matter.
AHP also argues that the objective of the MDS-96 protocol is
indistinguishable from another protocol which AHP identifies as an
``FDA/Industry protocol.'' (AHP Exceptions at 32-33.) AHP, citing
exhibit G-6, argues that document is a protocol drafted by the
pharmaceutical industry in conjunction with FDA, and that the protocol
used in the MDS-96 study is comparable. (AHP Exceptions at 32-33.) The
Center argues that AHP is incorrectly characterizing this document as
an ``FDA/Industry protocol,'' and the Center further argues that the
document is actually a protocol from another study, the MDS-176 study,
performed by Dr. Reich as part of the multicenter Five-center study,
the second study submitted by AHP in support of the intermittent
claudication indication for Cyclospasmol. (Center Response to
AHP Exceptions at 15.) I find that the Center is correct in its
argument.
I therefore conclude that the ALJ was correct in finding that the
MDS-96 study did not clearly state its objectives.
b. Test for presence of the disease. The ALJ ruled that patient
selection in the MDS-96 study was marred because the study lacked an
objective test to determine the presence of intermittent claudication.
(I.D. at 23, 55.) AHP argues that the ALJ did not express his views as
to what he concluded were the shortcomings of evaluating patients for
intermittent claudication on the basis of a personal history and a
physical examination, the latter which included the palpation of
pulses. (AHP Exceptions at 38.) In a related argument, AHP charges that
the ALJ did not give his rationale for concluding that some type of
objective instrumentation should have been used to make the diagnosis
of intermittent claudication. (AHP Exceptions at 40.) I disagree with
AHP's characterization of the ALJ's opinion.
It must be noted that the Reich study's protocol did not require
the patients to have intermittent claudication as a condition of
entering the study. Rather, under the protocol, patients included in
the Reich study were to have a diagnosis of peripheral vascular
disease, with one or more of the following symptoms:
[[Page 64104]]
Intermittent claudication, rest pain, cold extremities, or peripheral
cyanosis. (G-25.2 at 163.) Intermittent claudication was mentioned only
as one symptom among a number of symptoms of peripheral vascular
disease which patients entering the study could have.
I further note that while ``claudication'' was marked on most
patient forms as a symptom reported by the patient, intermittent
claudication was not listed in the physician's diagnosis for most
patients. In fact, only one patient had intermittent claudication
marked as a diagnosis. (G-29.1 at 16.) Most other patients had a
diagnosis of arteriosclerosis obliterans.
However, even assuming for the moment that intermittent
claudication was the physician's diagnosis, my review of the patients'
forms nevertheless reveals a number of instances where it is not at all
clear that the patient in fact had intermittent claudication. For
example, rest pain is an indication that the patient has a condition
other than intermittent claudication. (See Reich, Tr. Vol. V at 17, 58
(speaking generally about intermittent claudication).) Dr. Scheiner, an
AHP witness, testified that patients with rest pain were excluded from
the study (Scheiner, Tr. Vol. V at 14), but this does not appear to be
the case. A review of the records reveals that at least four patients
had ``rest pain'' checked as a symptom on their case records (G-29.1 at
21, 34, 46, 82), and a fifth patient had a question mark entered into
the box for rest pain on the case record. (G-29.1 at 65.) A sixth
patient had night cramps in calves listed as a symptom (G-29.1 at 5),
which is also distinct from intermittent claudication.
Additionally, another patient was diagnosed as having Raynaud's
syndrome, and not intermittent claudication. (G-29.1 at 21.) Also, two
patients accepted into the study, Patient Nos. 39 and 62, had
ulceration marked as a symptom (G-29.1 at 42; G-29.1 at 75), which in
itself can be a cause of pain and which was a basis for exclusion under
the protocol. (G-25.2 at 163.) While one of these two patients with
ulcerations, Patient No. 39, was excluded at the completion of the
study for failure to follow the medication regimen, I note that the
existence of this patient's leg ulcerations was not discussed. (G-29.1
at 4.) The other patient with reported leg ulcerations, Patient No. 62,
remained in the study.
The problem with the patient histories for the Reich study is that
these histories are not well documented. The patient histories do not
provide sufficient information to support the diagnosis of intermittent
claudication. For example, as previously discussed, although several
patients complained of rest pain, these patients were included. Dr.
Reich testified that these patients ``may have pains at night, and this
is certainly rest pain of sorts but it is not ischemic neuritic rest
pain.'' (Reich, Tr. Vol. V at 58.) However, there is nothing in the
patient records which reveals how this diagnosis was made. The patient
records do not elaborate on the type of rest pain which the patients
experienced, and so this aspect of the study cannot be reviewed.
Regarding the necessity in a clinical study for documentation
supporting a diagnosis, Dr. Lipicky, a witness for the Center,
testified:
The protocol did not specify the diagnostic aspects of the
disease. Ordinarily, if one is doing a specific hypothesis testing
protocol, the diagnostic criteria would be explicitly laid out. * *
* * Such specificity was lacking from the protocol under question.
From an overall point of view, the inclusion of patients was
entirely dependent upon the clinical judgment and the clinical
opinion of the investigator. No documentation of the validity of
that opinion was made available. This is not acceptable.
(Lipicky, G-61 at 6 (emphasis added).)
I find that the reliability of the diagnosis of intermittent
claudication for the patients in the Reich study was properly called
into question, and that the ALJ was correct when he ruled that ``(t)he
method of patient selection failed to limit entry into the study to
patients with intermittent claudication. This could easily have been
rectified with the use of an objective test to determine the presence
of the condition under review.'' (I.D. at 55.)
Additionally, further tests were needed to confirm the diagnosis of
intermittent claudication because there are other conditions which may
present as intermittent claudication arising from arteriosclerosis
obliterans, but in actuality be another disease or condition. Regarding
this point, Dr. John Vyden, a witness for the Center, testified:
Over half of the patients that I have seen in my professional
career, which amounts to thousands of patients sent to me for
investigation of intermittent claudication, do not in fact have
intermittent claudication. The commonest cause of full leg pain is,
in fact, degenerative joint disease of the (lumbar) spine and
sciatic nerve radiation.
(Vyden, G-59 at 7 (emphasis added).)
Specifically with regard to the Reich study, Dr. Vyden testified:
A major problem with this study is that there is no evidence
that these people really suffered from intermittent claudication. By
this I mean that they should have been tested by the technique named
oscillometry to insure that, in fact, they did have narrowing of the
arteries in the legs. The feeling of pulses is not an adequate
substitute because it is misleading. One must actually examine by
oscillometry the status of the arteries in the thighs and legs to
see whether in fact there is arterial disease in the person or not.
(Vyden, G-59 at 6-7.)
AHP argues that Dr. Vyden's testimony should not be credited
because oscillometry, the type of instrument which was identified by
Dr. Vyden as an objective measure of intermittent claudication, is an
outmoded technique. AHP's arguments do not change my ruling.
Firstly, AHP's argument fails to address the main point of Dr.
Vyden's testimony, i.e., that a common cause of full leg pain is
degenerative joint disease of the lumbar spine and sciatic nerve
radiation. This is a possible confounding factor to the Reich study.
Secondly, Dr. Reichle, a witness for AHP who criticized
oscillometry as outmoded, conceded that he, too, had used oscillometry
as recently as 1 year before the Reich study was conducted. (Tr. Vol.
II at 14.) While oscillometry may have been eclipsed by newer
technology, such as the Doppler, I note that this does not diminish Dr.
Vyden's main point, i.e., that an objective test was needed to confirm
a suspected diagnosis of intermittent claudication.
FDA regulations require adequate assurance that patients have the
disease or condition being studied. (Sec. 314.126(b)(3).) As was ruled
in the Commissioner's Decision regarding the drug Cothyrobal,
``Clearly, a study * * * must be conducted in patients who have one of
the labeled indications if that study is to be used a proof of
effectiveness for those indications.'' (Commissioner's Decision on
Cothyrobal, 42 FR 28602 at 28610.) Therefore, I find no error in the
ALJ's ruling on this basis.
AHP next argues that the ALJ did not consider Dr. Reich's testimony
in which he stated that he had tested the MDS-96 study patients with a
Doppler instrument even though that was not required by the protocol.
(AHP Exceptions at 39-40; Reich, Tr. Vol. V at 61-62.) On this point,
Dr. Reich testified:
Every patient had a Doppler study in the MDS- 96 study, every
single one of them. * * * As a matter of fact, you know, in the '70s
when this was being done, in the early '70s, the Doppler was just
being introduced for this sort of a measurement. I was using the
Doppler for at least ten years earlier than that. In the '70s they
were coming out with commercial instruments. Now, blood pressure--
you know, measuring ankle blood
[[Page 64105]]
pressure was just being introduced in clinical medicine and, as I
say, the cheap Doppler instruments--the low cost Doppler instruments
were being made available and I was doing this just out of curiosity
to see how my numbers would stack up with other people's. You know,
there was no big clinical mass of data to evaluate the significance
of it but I have Doppler measurements on all of my patients,
probably going back about 16--
(Question from the Center's Attorney): Did you report the
Doppler measurements?
(Answer from Dr. Reich): No, the protocol didn't call for it--
not the protocol but the report sheet didn't have a thing but I have
it in my own records.
(Reich, Tr. Vol. V at 61-62 (emphasis added).)
As is clear from Dr. Reich's testimony, no written reports were
submitted to the Center to show what values were obtained with the
Doppler and what criteria were used to determine whether the patients
had intermittent claudication. FDA regulations require that the report
of a study ``provide sufficient details of study design, conduct, and
analysis to allow critical evaluation and a determination of whether
the characteristics of an adequate and well-controlled study are
present.'' (Sec. 314.126(a).) I find that the mere fact that Dr. Reich
obtained some Doppler measurements for patients in the study to be of
no moment if those measurements were never recorded in the study
results, nor submitted to the Center for review, nor were in evidence
before the ALJ for his consideration. For this reason, I find no error
in the ALJ's decision on this matter.
AHP further argues that the ALJ erred when he considered Dr. Travis
V. Winsor's testimony regarding a previous, similar study that Dr.
Winsor conducted in 1972. (AHP Exceptions at 41-43.) Specifically, Dr.
Winsor testified that in 1972 he conducted a study which required, in
addition to the clinical estimation of the patient's condition at
baseline, an objective evaluation of the pulse volume by segmental
plethysmogram obtained at one wrist and both ankles. (Winsor, Tr. Vol.
III at 105.) A segmental plethysmogram was not performed in the MDS-96
study. The ALJ found that the implication was that the MDS-96 study
protocol was deficient in not requiring some form of objective
evaluation. (I.D. at 15.) AHP challenges this conclusion.
I find no error in the ALJ's reliance on this evidence as one of
the factors in his decision. Dr. Winsor's testimony regarding this
matter was in evidence (Winsor, Tr. Vol. III at 105), as was a copy of
the protocol for that study. (G-25.2 at 176-180.) This evidence was
available for the ALJ's review, and I find that his use of it was
proper.
Based on my review of the evidence, I find that the ALJ's
conclusion is supported by the evidence. The ALJ's conclusion that the
MDS-96 study should have included an objective test for the presence of
intermittent claudication was correct. Therefore, I find no error in
the ALJ's ruling.
c. Foot pedal ergometer as an evaluative measure. The ALJ
determined that the evidence was insufficient to show that the foot
pedal ergometer was a useful measure of Cyclospasmol's
efficacy in treating intermittent claudication. (I.D. at 18-21, 56.)
AHP takes several exceptions to the ALJ's ruling on this matter. (AHP
Exceptions at 48-53.) (AHP also disputes the ALJ's findings with regard
to the Winsor study, which was a study submitted by AHP to show the
correlation between the foot pedal ergometer measurements and treadmill
measurements. I will discuss the Winsor study separately in section
I.C.1.d. of this document.)
First, to reiterate the specifications of the Reich protocol
regarding the foot pedal ergometer, the protocol provided that blood
flow was to be measured both with the patient at rest in a recumbent
position, and after the patient exercised on a foot pedal ergometer.
(G-25.2 at 164.) Exercise on a foot pedal ergometer was performed by
the patient in a supine position, with the patient using his or her
foot to repeatedly raise a weight attached to a foot pedal. (Reich, A-
112 at 29; see also Denton, A-121 at 3-4.) Exercise on the foot pedal
ergometer was to be continued until claudication or, if pain did not
appear, was to be discontinued after 500 plantar flexions of the foot.
(G-25.2 at 164.) The protocol further stated that vasomotor reflexes of
the leg and calf blood flow were to be measured at the beginning of the
study and at 2-week intervals during the study by means of venous
occlusion plethysmography with a mercury-in-rubber strain gauge. (G-
25.2 at 164.)
In AHP's first objection on this point, AHP questions ``what the
ALJ's basis'' was for ruling that the foot pedal ergometer used in the
Reich study was not an accurate predictor of walking ability. (AHP
Exceptions at 48.) The basis for the ALJ's decision is set forth in the
Initial Decision. More important, however, is the question of whether
the evidence was sufficient to support AHP's claim that the foot pedal
ergometer was an accurate predictor of walking ability, and it appears
that this is the issue which AHP is arguing and which I will address.
In considering this issue, I have reviewed the ALJ's decision, and
I find that the ALJ adequately summarized the evidence on both sides of
the issue before making his ruling. (I.D. at 18-20.) This evidence
included the testimony of Drs. Vyden and Lipicky, witnesses for the
Center, who both testified that the foot pedal ergometer was not shown
to be an accurate predictor of walking distance. (Vyden, G-59 at 9;
Lipicky, Tr. Vol. IV at 60-66.) Specifically, Dr. Vyden testified:
A foot ergometer, in my judgment, is not a satisfactory testing
device (as compared to a treadmill) on whether a drug is effective
in treating intermittent claudication. Now the reason for this is
that, let us say we have a patient who is 150 pounds. That patient
has to walk and support 150 pounds of weight when walking. It is a
total bodily exercise. Now, when they are using the ergometer they
are, in fact, not measuring the leg muscle when it is supporting the
entire body weight. Therefore, the amount of work being done on the
ergometer does not reflect whether a patient can walk further since
most of their body is not being used in this exercise.
(Vyden, G-59 at 9.)
Similarly, when Dr. Lipicky was asked to comment on the use of the
foot pedal ergometer as a measure of efficacy, he testified that while
the foot pedal ergometer was a measure of the ability of the muscles to
perform certain work, the foot pedal ergometer measurement was
different from walking in that the patient using the foot pedal
ergometer was not required to support the body's weight while
exercising. (Lipicky, G-61 at 9.)
Witnesses for AHP expressed the view that the foot pedal ergometer
was a valid indication of efficacy for Cyclospas-
mol . (Reichle, A-110 at 4-5; 2 Winsor, A-111 at 5;
Reich, A-112 at 30- 31; Porter, A-109 at 7-8; Scheiner, A-122 at 2-3;
Denton, A-121 at 3-4.) However, I note that none of the AHP witnesses
can be said to have refuted the basic point of the testimony of the
Center's witnesses, that being that work on a foot pedal ergometer is
different from walking because walking entails more of the
cardiovascular system, in addition to the joints and skeletal system,
and requires a person to carry the weight of his or her body while
exercising. I note that the testimony given by AHP's witnesses is
consistent with the testimony of the Center's witnesses on this point.
For example, Dr. Winsor, an AHP witness, testified as follows:
2 The Dockets Management Branch used the letter ``A'' to
refer to the exhibits of Ives Laboratories, a wholly owned
subsidiary of American Home Products.
---------------------------------------------------------------------------
Ergometry and treadmill testing are different in some respects.
Exercising on a
[[Page 64106]]
treadmill increases the cardiac output and this increased cardiac
output helps the circulation of blood in the leg. Exercising on an
ergometer, however, does not have a significant cardiac aspect to
it. The ergometer measures the ability of a set of muscles to
perform work with a near constant cardiac participation, but
exercising on a treadmill involves both cardiac and peripheral
---------------------------------------------------------------------------
circulation.
(Winsor, A-111 at 5.)
Similar testimony was given by Dr. Porter, another AHP witness, who
expanded on the differences between the foot pedal ergometer and the
treadmill as follows:
The correlation (between the ergometer and the treadmill) will
not be one-to-one for two reasons. First, the patient's ability to
perform work on a treadmill will vary somewhat from day to day
depending on a variety of physical and emotional factors, such as
whether the patient got a good night's sleep and whether he is angry
or depressed. Second, the ergometer focuses on the capacity of two
muscles, the gastrocnemius and the soleus muscles, to perform work.
While the treadmill involves principally the use of the
gastrocnemius and soleus muscles, it also involves the use of other
muscles in the body and of the patient's cardiovascular system.
These other muscles and the cardiovascular system may affect a
patient's conclusion as to when he feels forced to stop walking on a
treadmill.
(Porter, A-110 at 8.)
I find that the difference between the testimony of the Center's
witnesses and of AHP's witnesses lies in their disparate views as to
whether the limits of the focus of the foot pedal ergometer was a
positive factor because it isolated the work of certain muscles, or
whether the foot pedal ergometer exercise was so dissimilar from the
actual outcome of interest, i.e, walking ability, that the foot pedal
ergometer could not be said to be a useful measure of a patient's
walking ability.
The ALJ, after reviewing the evidence presented by both parties,
ruled:
(T)he suitability of the ergometer as a measurement of walking
ability is called into question since a treadmill is more commonly
used in studies where the relevant function to be tested is walking.
Thus if the ergometer is to be used as a measurement of walking
ability, some basis is needed to correlate these factors.
(I.D. at 20.)
I find the ALJ's ruling to be sound. As stated previously in this
section, the evidence indicates that exercise on a foot pedal ergometer
is different in many respects from walking. Therefore, I find that the
evidence offered by AHP, in which witnesses described their personal
experiences with ergometers and expressed their own estimations that a
foot pedal ergometer was an accurate measure of walking ability, was
insufficient to show that the foot pedal ergometer was a useful measure
of Cyclospasmol's efficacy in treating intermittent
claudication, absent other sufficient evidence demonstrating such a
correlation. (Again I note that the Winsor study, which was offered by
AHP for the purposes of correlating the foot pedal ergometer with
walking on a treadmill, will be discussed in a subsequent section of
this decision. (See section I.C.1.d. of this document.))
AHP further argues that the ALJ did not consider the views of three
AHP witnesses who testified regarding the foot pedal ergometer, Drs.
Reichle, Scheiner, and Denton, and that the ALJ mischaracterized the
views of three other AHP witnesses, Drs. Porter, Winsor, and Reich.
(AHP Exceptions at 49.)
Regarding the testimony of Drs. Reichle, Scheiner, and Denton, I
note that the ALJ is not required to make findings on all the evidence
when the findings which the ALJ has made support the ALJ's decision.
(See Immigration and Naturalization Serv. v. Bagamasbad, 429 U.S. at
25; Deep South Broadcasting Co. v. FCC, 278 F.2d at 266; Community &
Johnson Corp. v. United States, 156 F. Supp. at 443.) Also, as has been
established in prior cases, the ALJ is not required to accept the
opinion of expert witnesses. (Warner-Lambert Co. v. Heckler, 787 F.2d
at 154; Commissioner's Decision on OPE, slip op. at 22; Commissioner's
Decision on Deprol, 58 FR 50929 at 50930.) Such testimony is only as
strong as the studies upon which it is based. (Commissioner's Decision
on OPE, slip op. at 22, citing Upjohn Co. v. Finch, 422 F.2d 944 (6th
Cir. 1970).)
Regarding the testimony of Drs. Porter, Winsor, and Reich, AHP
argues that the ALJ mischaracterized their testimony by failing to make
it clear that these witnesses testified that they had used ergometry
extensively and had testified without qualification that they believed
the foot pedal ergometer was a reliable predicator of walking ability.
(AHP Exceptions at 50.) I have reviewed the testimony of these
witnesses, and I do not find that their testimony changes my ruling
regarding the foot pedal ergometer used in the Reich study. As I stated
previously, the testimony of AHP's witnesses is consistent with the
testimony of the Center's witnesses, in which the latter testified that
the foot pedal ergometer exercise was different in several key respects
from the exercise of walking. Therefore, I find that the ALJ was
correct in ruling that the suitability of the foot pedal ergometer as a
measurement of walking ability was not established, and that a
correlation between the foot pedal ergometer and walking ability needed
to be demonstrated.
AHP also takes exception to the ALJ's decision on the grounds that
the ALJ did not expressly state how much weight he gave to the
testimony of the Center's witnesses who testified against the foot
pedal ergometer as an evaluative measure. (AHP Exceptions at 51.) AHP
offers no legal authority as a basis for asserting that the ALJ must
expressly assign a weight to the testimony of witnesses, and I find
this argument to be without merit. As I stated in a previous paragraph,
the ALJ is not required to make findings on all the evidence when the
findings which have been made support the decision. (See Immigration
and Naturalization Serv. v. Bagamasbad, 429 U.S. at 25; Deep South
Broadcasting Co. v. FCC, 278 F.2d at 266; Community & Johnson Corp. v.
United States, 156 F. Supp. at 443.)
AHP further avers that the ALJ mischaracterized the Center's
position on the use of the foot pedal ergometer when the ALJ wrote,
``However, the Center believes that the ergometer measurement is not an
accurate predictor of walking distance since walking is a `total bodily
exercise.' '' (I.D. at 18-19, citation omitted.) I find this objection
to be without merit, since the ALJ correctly quoted the testimony of
Dr. Vyden, the Center's witness. (Vyden, G-59 at 9.)
For the above reasons, I conclude that the ALJ did not err in his
consideration of the testimony of AHP's experts regarding the foot
pedal ergometer.
d. The Winsor study. The Winsor study was an additional study
performed by AHP for the purpose of correlating measurements taken on a
foot pedal ergometer with measurements taken on a treadmill. (Winsor,
A-111 at 4-6; A-124 at 31-44.) The Winsor study did not have a written
protocol. The subsequent report on the study indicated that 13 patients
were tested on both a foot pedal ergometer and on a treadmill. (A-124
at 31; AHP Post-Hearing Brief at 21.) It was reported that the two
tests were carried out 30 minutes apart. The report stated that
patients were randomized with respect to the order of the two tests.
(Winsor, A-111 at 7; A-124 at 31.)
Of the 13 patients in the Winsor study, 4 patients were brought
back for a second day of tests. One patient, Patient No. 2, was
reported to have had the concomitant condition of arthritis in the
knee, and it was further reported that at the patient's first test,
arthritis affected this patient's performance. For this reason, Dr.
Winsor decided that
[[Page 64107]]
Patient No. 2's first test results would not be used in the statistical
analysis. (A-124 at 31.) Instead, this patient's second day test
results on both the ergometer and the treadmill were used in the
statistical analysis. (A-124 at 31.)
The other three patients who were tested twice--Patient Nos. 8, 9,
and 12--were reported to have had peripheral vascular disease in both
legs. For this reason, Dr. Winsor decided to retest these three
patients on a second day on both the ergometer and the treadmill, using
the other leg on the ergometer. (A-124 at 31.) In the subsequent
statistical analysis, results for these three patients were analyzed in
three ways. Initially, the first day test results of these patients
were used in the analysis. (A-124 at 32.) Next, the results were
reanalyzed twice more, once using these patients' lowest reported
ergometer test results, and then using these patients' highest reported
ergometer test results. (A-124 at 32.) As for the treadmill results, it
appears that the treadmill readings taken on the same day as the
corresponding ergometer results were used. (A-124 at 32; 36.)
The post-study report stated that there was a ``significant
correlation'' between the treadmill distance and ergometer foot-pounds.
(A-124 at 32.) The ALJ, describing the Winsor study as hastily
organized and conducted, ruled that the study was not adequate to prove
that the foot pedal ergometer was a useful measure of the efficacy of
Cyclospasmol for intermittent claudication. (I.D. at 56.) AHP
disputes the ALJ's conclusions. (AHP Exceptions at 53-72.)
As one of its objections, AHP asks whether the ALJ gave any weight
to the Center's contention that the Winsor study should be disregarded
because it was not carried out under a written protocol. (AHP
Exceptions at 58-59; see Center Post-Hearing Brief at 28.) While the
ALJ did not expressly make a ruling on this point (see I.D. at 19), I
find that the fact that the Winsor study lacked a written protocol is a
matter properly considered in evaluating and weighing the Winsor study.
The Winsor study was not a study to prove efficacy, and therefore,
strictly speaking, was not bound to comply with all of the requirements
for an adequate and well-controlled study, such as blinding. In this
respect, the Winsor study is comparable to a safety study, which
similarly does not necessarily have to satisfy every requirement of an
adequate and well-controlled clinical trial. (Commissioner's Decision
on Cothyrobal, 42 FR 28602 at 28614; Commissioner's Decision on Deprol,
58 FR 50929 at 50942.) Nonetheless, safety studies and, by the same
reasoning, supportive studies such as the Winsor study, must be
adequately designed so that scientists can draw reasonable conclusions
from them. (Commissioner's Decision on Cothyrobal, 42 FR 28602 at
28614.) For this reason, all of the factors that are relevant to a
determination as to whether an efficacy study is adequate and well-
controlled are also relevant in determining whether other supportive
studies are adequate for their purposes. (Commissioner's Decision on
Deprol, 58 FR 50929 at 50942 n.5.)
One of the most basic requirements for a study is a written
protocol. The regulations provide that ``the protocol for the study * *
* should describe the study design precisely * * *.'' (Sec. 314.126
(b)(2).) As is noted in the regulations, this characteristic, along
with the other characteristics set forth in this section of the
regulations, has been developed over a period of years and is
recognized by the scientific community as an essential of an adequate
and well-controlled clinical trial. (Sec. 314.126(a).) The written
protocol should have included a summary of the proposed or actual
methods of analysis and a description of the method of selection of
subjects. (Sec. 314.126 (b)(1) to (b)(7).) The necessity for a written
protocol is clear. It is a key factor in preventing bias, whether
intentional or unintentional, from influencing a study's outcome. The
problems created by the absence of a written protocol can be seen in
the Winsor study. For example, Dr. Winsor retested one of the patients
after noting an ``abnormality'' in the patient's first test results, an
abnormality said to be attributed to the subject's arthritis. Dr.
Winsor also tested three patients in a different manner from the rest,
by testing each leg separately on the foot pedal ergometer. (I.D. at
19.) These types of variations in testing among patients raise serious
questions of bias, and the questions of bias are only exacerbated by
the absence of a written protocol describing the testing protocol.
Also, because of the absence of a written protocol, the basis for
patient selection was not set forth in advance of the Winsor study.
While the post-study report stated that all patients in the Winsor
study had intermittent claudication, the report failed to describe the
basis for this diagnosis. AHP argues that it was not necessary to have
a written protocol describing the selection criteria since Dr. Winsor
was familiar with all of the patients' conditions because he had been
the patients' doctor for quite some time. (AHP Exceptions at 65.) The
regulations state that the method of selecting subjects for a study
should provide adequate assurance that the subjects have the disease or
condition being studied. (Sec. 314.126(b)(3).) I do not find the
undocumented, prestudy experience of Dr. Winsor with the study patients
to be sufficient evidence of the patients' conditions.
AHP next challenges the ALJ's opinion on the grounds that the ALJ
did not state what he understood to be Dr. Lipicky's central criticism
of the Winsor study. (AHP Exceptions at 66-67.) AHP further questions
whether the ALJ understood the Winsor study, the focus of this argument
being whether the ALJ should have given any weight to Dr. Lipicky's
testimony in which Dr. Lipicky questioned aspects of the Winsor study.
(AHP Exceptions at 70-72.)
Dr. Lipicky testified at some length regarding the Winsor study.
One of the aspects of Dr. Lipicky's testimony which AHP is challenging
is Dr. Lipicky's review of certain graphs drawn by Dr. Wang, an AHP
witness, based on the data points from the Winsor study. (AHP
Exceptions at 71; AHP Post-Hearing Brief at 22-24.) As part of its
post-study report, AHP submitted several graphs plotting the results of
the Winsor study. (A-124 at 38-44.) Of particular focus in the present
issue are two graphs plotting treadmill feet versus ergometer foot-
pounds.3 (A-124 at 42-43.) These graphs are of interest because
the post-study report stated that there was ``significant correlation
between treadmill distance and ergometer ft-lb.'' (A-124 at 32.)
---------------------------------------------------------------------------
3 The other graphs plotted ergometer foot-pounds versus
treadmill foot-pounds. (A-124 at 38-41.) There was also a scatter
diagram plotting treadmill foot-pounds/minute versus ergometer foot-
pounds/minute. (A-124 at 14.)
---------------------------------------------------------------------------
As described in the post-study report, ``Regression of the work
performed (was) carried out using linear regression with or without
forcing through the origin (i.e. assume that if the ergometer work is
zero, the treadmill work should also be zero).'' (A-124 at 32.) In
other words, a straight-line graph was plotted which most closely fit
the data points, and another straight-line graph was plotted forcing
the graph through the origin of the graph. Regarding the former of
these two graphs, Dr. Lipicky had testified that the graph ``says that
when a patient cannot pump an ergometer that patient can walk 200 ft,
which clearly is a nonsensical result. It defies common sense that that
would be the case.'' (Lipicky, Tr. Vol. IV at 64.) Regarding the graph
forced through the origin, Dr. Lipicky testified, ``most of the data
points, (especially) the early ones, are well above that line and a
couple of
[[Page 64108]]
data points later on lie well below that line--to my eye, not a very
good fit at all.'' (Lipicky, Tr. Vol. IV at 64.)
Using the same data points, Dr. Lipicky drew and offered several
other possible graphs. (G-67 at 2-4.) Dr. Lipicky cited one of his
graphs in particular as fitting the data points best of all. In this
graph, the line began at slope, the slope then decreased and at one
point flattened out for the later data points. (G-67 at 2-3.)
AHP criticizes Dr. Lipicky's testimony on several grounds. First,
AHP argues that Dr. Lipicky is essentially testifying that the Winsor
study was deficient because it did not yield a mathematical formula
that described the relationship between the foot pedal ergometer
measure and the treadmill measure. (AHP Post-Hearing Brief at 22.) AHP
argues that Dr. Lipicky's testimony on this point is faulty because he
did not disclose why such a mathematical formula would be useful. I
disagree with AHP's position.
Dr. Lipicky testified that the issue raised by the results of the
Winsor study was what is ``the explicit relationship between the two
variables. Given a specific ergometer value, whatever its units, what
can one predict would be the walking distance on (the) treadmill in the
absence of having measured it?'' (Lipicky, Tr. Vol. IV at 124.) In
considering this evidence, it must be kept in mind that the Winsor
study was undertaken to supplement the MDS-96 study, since the results
of the MDS-96 study were expressed in terms of foot pedal ergometer
units, despite the fact that other evidence indicated that the
treadmill is more commonly used. For this reason, I find that Dr.
Lipicky was correct in noting that it was necessary for the Winsor
study to demonstrate the value of the foot pedal ergometer to predict
walking distance on a treadmill.
AHP further argues that Dr. Lipicky's testimony should not be
credited because the graphs which he submitted, in particular the graph
described in the above discussion as flattening-out, reflects only Dr.
Lipicky's hypothesis. (AHP Post-Hearing Brief at 22-23.) AHP argues
that Dr. Lipicky's testimony fails because Dr. Lipicky offered no
physiological or other explanation to explain why his graph of the data
points shows that a person might be able to increase his or her
performance on the foot pedal ergometer without correspondingly
increasing his or her performance on the treadmill. (AHP Post-Hearing
Brief at 22-24.)
I find that Dr. Lipicky's testimony indicates that the data may be
interpreted in more than one way. Indeed, Dr. Lipicky stated in his
testimony that his graphs represented ``an alternate way of looking at
the same data and that there's no way from that data to choose between
those two interpretations.'' (Lipicky, Tr. Vol. IV at 65; see I.D. at
20.) As Dr. Lipicky noted, while there may be some relationship between
the foot pedal ergometer and the treadmill, the crux of the matter at
issue lies in defining the relationship between the two. (Lipicky, Tr.
Vol. IV at 65, 124.)
Dr. Lipicky offered testimony indicating that the graphs submitted
by AHP either did not fit the data results or suggested a result that
did not make sense. The graphs submitted by Dr. Lipicky reflected a
better fit with the data. Why the Winsor study's data came out as they
did was not an issue which Dr. Lipicky was required to explain. While
Dr. Lipicky, as a witness for the Center, suggested several possible
other graphs, the Center does not have the burden of proof. AHP has the
burden of proving the nature of the relationship, if any, between the
results on the treadmill and the results on the foot pedal ergometer.
The correlation between the two measures needed to be defined, and the
burden of proof lay with AHP as proponent for approval of the efficacy
of Cyclospasmol. (Weinberger v. Hynson, Westcott & Dunning,
412 U.S. 609, 617 (1973), citing 21 U.S.C. 355(e)(3).) Therefore, I
find no merit in AHP's argument.
AHP also contends that the ALJ devoted only two sentences of his
opinion to the Winsor study. (AHP Exceptions at 71.) As I previously
discussed, the ALJ gave adequate reasons why he did not credit the
Winsor study. Also, the ALJ devoted several pages of his opinion to a
review of the Winsor study. (I.D. at 19-21, 23, 56.) I find that the
evidence supports a finding that the ALJ did understand the Winsor
study, and I affirm his decision with respect to it.
AHP further argues that the ALJ did not indicate how much weight he
gave to the following arguments of the Center: (1) That the Winsor
study should be disregarded because it was not carried out pursuant to
a written protocol, (2) that the Winsor study should be disregarded
because Dr. Winsor undertook the study after he had agreed to be a
witness for AHP, (3) that Dr. Winsor retested 4 of the patients, and
(4) that although it was reported that the patients in the study had
intermittent claudication, there was no objective evidence that the 13
patients in the Winsor study had intermittent claudication. (AHP
Exceptions at 58-66; see Center Post-Hearing Brief at 27-30.) There is
no rule in law or regulations which requires the ALJ to explicitly
assign a weight to the evidence which the ALJ considers. As I
previously stated, the ALJ is not required to make findings on all the
evidence when the findings which have been made by the ALJ support the
decision. (See Immigration and Naturalization Serv. v. Bagamasbad, 429
U.S. at 25; Deep South Broadcasting Co. v. FCC, 278 F.2d at 266;
Community & Johnson Corp. v. United States, 156 F. Supp. at 443.)
AHP further questions the ALJ's conclusions that the suitability of
the foot pedal ergometer as a measure of walking ability was called
into question because the treadmill is more commonly used, and that if
the foot pedal ergometer was to be used, some basis was needed to
correlate these two measures. (AHP Exceptions at 68-69.) I addressed
this issue in section I.C.1.c. of this document, wherein I ruled that
it was necessary to correlate the measures taken on the treadmill with
measures taken on the foot pedal ergometer because the evidence
indicated that the foot pedal ergometer exercise was different in
several key respects from the exercise of walking on a treadmill.
In my judgment, the ALJ was correct in concluding that AHP did not
prove that the foot pedal ergometer was useful in demonstrating
Cyclospasmol's efficacy in treating intermittent
claudication. I find sufficient justification to support the ALJ's
rejection of the Winsor study.
e. Adequacy of the MDS-96 (Reich) study. In sum, I find that the
Reich study was not adequate and well-controlled. In making this
determination, I have considered the aggregate effect of the protocol
violations. As I previously discussed: (1) The objective of the study
was vague and the protocol was not clear in identifying intermittent
claudication as the focus; (2) the reliability of the diagnosis of
intermittent claudication was properly called into question and an
objective test for intermittent claudication should have been included
in the study; and (3) the evidence did not establish that the foot
pedal ergometer was a suitable measure of walking ability.
Regarding the Winsor study, I find that the ALJ properly concluded
that AHP did not prove that the foot pedal ergometer was useful in
demonstrating Cyclospasmol's efficacy in treating
intermittent claudication. As detailed above: (1) The Winsor study did
not have a written protocol; (2) not all patients in the study were
tested in the same manner; (3) the basis for patient selection was not
set forth in advance of the study; and (4) the study did not
[[Page 64109]]
demonstrate the value of the foot pedal ergometer in predicting walking
distance on the treadmill.
2. The Five-Center Study
The five-center study was, as its name indicates, a multicenter
study conducted at five sites. The study's stated objective was to
``evaluate the efficacy of Cyclospasmol versus placebo, as an
adjunct to generally accepted therapy, for the amelioration of symptoms
(including intermittent claudication) in the lower extremities of
patients with chronic occlusive arterial disease (atherosclerosis) who
have no manifestations of severe (advanced) disease * * *.'' (G-6 at
3.) Severe disease was defined in the protocol as:
severe (advanced) chronic occlusive arterial disease as
manifested by major trophic changes (e.g., atrophic shiny skin,
major nail changes and/or muscle atrophy), ischemic rest pain,
ulceration and/or gangrene, marked pallor or rubor with the
extremity in the horizontal position. Also those in whom prior
arteriography has demonstrated combined aortoiliac and
femoropopliteal disease; or popliteal disease involving the
trifurcation; or distal arterial (tibial) disease or arteriolar
disease such as may be associated with diabetes mellitus.
(G-6 at 5-6.)
The five-center study employed a crossover design. (G-9.1 at 85.)
Initially, a 6 to 8 week, single-blinded placebo washout period was
used. (G-9.1 at 85.) Patients were then randomly assigned to one of two
groups in a double-blinded manner. Group I received a placebo for 12
weeks and then Cyclospasmol for 12 weeks, with no intervening
washout period. Group II underwent the reverse sequence, also with no
intervening washout period. (G-9.1 at 85.) One hundred and sixteen
patients were enrolled in the study, with 91 completing it. (G-9.1 at
85.) Of those who completed the study, 65 patients were adjudged to be
``acceptable,'' for analysis, i.e., capable of being evaluated. (G-9.1
at 85.)
Statistical analysis of the pooled data from the five centers
indicated no statistically significant difference between
Cyclospasmol and placebo. (G-9.1 at 86, 93, 142-46; AHP
Exceptions at 80.) The pooled data were then reanalyzed using only the
first half of the study (the initial 12 weeks) and the inclusion/
exclusion decisions for each patient were reconsidered. (A-108 at 1-
11.) Using one-tailed tests of significance, the reanalysis indicated a
statistically significant, drug-over-placebo effect. (A-108 at 1-11;
AHP Exceptions at 81.)
The ALJ ruled that the five-center study could not be considered
adequate and well-controlled, in part because the reanalysis of the
initial 12 weeks of the five-center study was performed only after the
failure to find a positive drug effect in the initial analysis. (I.D.
at 26, 30-31.) AHP has challenged the ALJ's findings on the following
matters: (1) The weight to be accorded the reanalysis of data, (2) the
inclusion and exclusion of patients, (3) the calculation of treadmill
distances, and (4) the inconsistency of results among the five centers
in the reanalysis. I address AHP's exceptions below.
a. Reanalysis of the five-center study. AHP takes exception to the
ALJ's conclusion that no weight should be given to the reanalysis of
the data from the five-center study. (AHP Exceptions at 78-88, citing
I.D. at 30, 56.) As previously discussed, the five-center study was
conducted using a crossover design. After statistical analysis of the
study failed to demonstrate a statistically significant difference
between drug and placebo (I.D. at 26; G-9.1 at 86), the data were
reanalyzed as if the study had been conducted with a parallel design.
(A-108 at 1-11.) To do this, the data from the second half of the
study--the final 12 weeks--were dropped. (Lipicky, Tr. Vol. IV at 68.)
Also, the decisions on inclusions and exclusions of all patients were
reexamined. (Issues pertaining to the reexamination of exclusions will
be discussed in section I.C.2.b. of this document.) AHP's reasons for
electing to perform this type of reanalysis were not communicated to
the Center, either orally or in writing. (Lipicky, Tr. Vol. IV at 68.)
In the reanalysis, a statistically significant improvement was reported
in the Cyclospasmol-treated group over the placebo group. (A-
108 at 3.)
In support of its decision to reanalyze the first 12 weeks of the
data as a parallel study, AHP cites to the testimony of Dr. Nathan
Mantel, a witness for AHP who was critical of crossover protocols in
general. (Mantel, A-127 at 10-12.) In relevant part, Dr. Mantel
testified:
When AHP turned to me for advice with respect to the proper
analysis of the five-center study, I voiced my own long-standing
criticism of use of a crossover design, albeit this is a design
greatly emphasized in standard statistical texts. Biological and
medical realities just do not correspond to the simple mathematical
model underlying use of the crossover. When a patient receives
treatment A, followed in due course by treatment B, the final
response observed is not a response to treatment B. Rather, it is a
response to the sequence of treatments used, including all lapses of
time. Another crossover design example, one not even involving any
initial values, is where half the patients get treated on the right
side with A, on the left side with B, these being switched for the
remaining half of patients. A crossover analysis could be invalid if
treatment on one side influenced the response on the other side.
(A-127 at 11.)
AHP further cites the testimony of Dr. Lipicky, a witness for the
Center, who testified that crossover studies are often analyzed as
parallel studies for the first half of the data, and that he himself
had probably spoken in favor of such analyses. (AHP Exceptions at 81,
citing Lipicky, Tr. Vol. IV at 92.) It is to be noted, however, that
Dr. Lipicky clarified his position in this regard by adding that, while
such reanalyses are a ``common practice,'' in his opinion it was very
often not an appropriate exercise. (Lipicky, Tr. Vol. IV at 94.) On
this point, Dr. Lipicky testified:
Well, I guess if one is talking about appropriateness, I think
that reanalyses are not appropriate very often--commonly done but
not appropriate very often; sometimes useful if, indeed, there are
particular things that one is trying to get to and if there is an
analysis that one can think of doing that, indeed, was not thought
of ahead of time and where the major intent of the trial is not
singularly or singly dependent upon that analysis.
(Lipicky, Tr. Vol. IV at 94.)
Other testimony on this issue was offered by Dr. Schneiderman, a
statistician and witness for the Center, who gave the following
testimony:
And, thus, in a cross-over experiment if a phase or a sequence
effect can be shown--a carry-over effect--then it would be
inappropriate, I think, to continue the analysis as if there were no
carry-over effect because that's one of the conditions, essentially,
from which you create a cross-over design. The original analysis of
these data did not show such a * * * carry-over effect and,
therefore, quite obviously it was appropriate to have designed the
experiment as it was designed and to continue to analyze it as the
indication had been for the analysis. I see no justification really
for discarding the cross-over design, which people who knew the
biology had designed, and, thus, discarding half the data.
(Schneiderman, Tr. Vol. VII at 5-6 (emphasis added).)
In addressing AHP's argument, I first note that it is a requirement
of an adequate and well-controlled study that there be an analysis of
the results of the study adequate to assess the effects of the drug.
(Sec. 314.126(b)(7).) Additionally, because faulty analysis can
introduce bias, adequate measures must be taken to minimize bias on the
part of the analysts of the data. (Sec. 314.126(b)(5).) Also, the
study's protocol should describe the study design precisely, including
information on the duration of treatment periods, whether
[[Page 64110]]
treatments are parallel, sequential, or crossover, and whether the
sample size is predetermined or based upon some interim analysis.
(Sec. 314.126(b)(2).) One of the most important reasons for requiring
protocol decisions to be made in advance of the clinical investigation
is to avoid bias.
As AHP acknowledged in its Post-Hearing Brief, FDA regulations
provide that a sponsor may use an analytical method that is not set out
in the protocol, but the sponsor should inform FDA as to how it
selected that analytical method. (AHP Post-Hearing Brief at 39;
Sec. 314.126(b)(1).) AHP did not inform the Center of the reasons for
switching from analyzing the entire data as a crossover study to
instead analyzing the first half of the study as a parallel study.
(Lipicky, Tr. Vol. IV at 68.) The testimony of Dr. Mantel fails as an
explanation because Dr. Mantel's reason for objecting to crossover
studies--specifically, the failure of patients to return to baseline at
the time of crossover (Mantel, A-127 at 10-12)--was not identified as a
problem with the five-center study. (See Schneiderman, Tr. Vol. VII at
5-6.) Moreover, AHP's reliance upon Dr. Mantel's broad indictment of
all crossover studies is difficult to accept, in view of the fact that
the second study submitted by AHP in support of the indication of
intermittent claudication for Cyclospasmol, the MDS-96 study,
was a crossover study and was analyzed as such by AHP. (See section
I.C.1. of this document.)
The reanalysis of the five-center study was more than a mere
mathematical check. It was a reconsideration of the protocol after the
clinical trial had been completed. While circumstances can arise that
justify analyzing only the first half of a crossover study as a
parallel study, such as when a sequence effect occurs, a decision to
throw out half of the data cannot be made arbitrarily if a study is to
be considered adequate and well-controlled. Where, as in the five-
center study, a ``reanalysis'' means that: (1) Initially no
statistically significant difference between the drug and the placebo
was found, (2) the inclusion and exclusion decisions for each patient
were reconsidered, (3) the second half of the crossover trial was
dropped, and (4) the first half of the crossover data was reviewed as
if the trial had been a parallel trial, then certainly the sponsor
should expect that an explanation for these changes would be in order.
AHP further challenges the ALJ's decision on the grounds that the
ALJ purportedly took the position that he would not consider a parallel
analysis of any study that is designed to gather data on a crossover
basis. (AHP Exceptions at 82-83, citing I.D. at 25.) The ALJ did not
make such a broad pronouncement. The ALJ rejected AHP's reanalysis
because AHP did not provide a ``good reason'' as to why AHP analyzed
only the first half of the data collected. (I.D. at 30.)
AHP also argues that the ALJ ignored evidence indicating that the
1985 reanalysis was precisely the type of analysis that the Center
itself would have required to establish efficacy. (AHP Exceptions at
84.) By this argument, AHP is apparently referring to the testimony of
Dr. Lipicky, a Center witness, who testified that crossover studies are
often analyzed as parallel studies, and that he himself had probably
spoken in favor of such a procedure. (Lipicky, Tr. Vol. IV at 92.)
However, as I noted above, Dr. Lipicky explained his position by adding
that while such reanalyses are commonly done in clinical studies, they
are very often not appropriate. I find AHP's interpretation of Dr.
Lipicky's testimony as a requirement for analysis of all crossover
studies as if these were parallel studies to be incorrect. Moreover, I
note that another witness for the Center, Dr. Schneiderman, was clearly
critical of AHP's reanalysis of this crossover study as a parallel
study. (Schneiderman, Tr. Vol. VII at 5-6.) In any event, regardless of
any statements by Dr. Lipicky, or any other witnesses for either party,
the Commissioner is not required to accept the testimony of expert
witnesses but is to make his or her own decision regarding efficacy.
(Warner-Lambert Co. v. Heckler, 787 F.2d at 154; Commissioner's
Decision on OPE, slip op. at 22; Commissioner's Decision on Deprol, 58
FR 50929 at 50930.)
AHP additionally argues that the ALJ erred in his understanding of
Dr. Schneiderman's testimony. (AHP Exceptions at 84.) AHP alleges that
Dr. Schneiderman did not indicate that the parallel analysis was
inappropriate, and that the ALJ erred in using Dr. Schneiderman's
testimony as part of his rationale for rejecting the reanalysis. I have
reviewed Dr. Schneiderman's testimony, and I find that the ALJ was
correct in his interpretation. Dr. Schneiderman's testimony could not
be more clear on this point, ``I see no justification really for
discarding the cross-over design, which people who knew the biology had
designed, and, thus, discarding half the data.'' (Schneiderman, Tr.
Vol. VII at 5-6.)
AHP further argues that the ALJ should have required the Center to
support its criticism of the reanalysis by preparing its own crossover
analysis using the values submitted by AHP in its reanalysis. (AHP
Exceptions at 86-87.) There is no basis in law for AHP's argument. The
burden of proving safety and efficacy lies with the applicant. (Hynson,
412 U.S. at 617; 21 U.S.C. 355(e); 21 CFR 12.87(e).) The Center,
therefore, was not obligated to perform its own crossover analysis,
particularly using the results as they were calculated in the
reanalysis in this case.
Notwithstanding my ruling on this issue, I nevertheless note that
the Center did perform an analysis using the original crossover data;
in this analysis, the Center followed the protocol for the five-center
study by using maximum, rather than average, treadmill measurements.
(G-71 at 1-4; Lipicky, Tr. Vol. V at 74-79.) However, this exhibit was
stricken on motion of AHP. (Tr. Vol. V at 6.) Additionally, I note
that, as Dr. Lipicky testified, in order for the Center to perform an
independent reanalysis, the Center would have to have access to the raw
data, i.e., the case report forms, and these were not submitted to FDA.
(Lipicky, G-61 at 19.)
AHP further contends that the ALJ erroneously concluded that AHP
had given no reason for submitting a parallel study. (AHP Exceptions at
87.) AHP is misstating the ALJ's decision. The ALJ held that AHP did
not provide a sufficient reason for its submission of a parallel
analysis for a crossover study. (I.D. at 30.) I uphold the ALJ's
conclusion.
AHP argues that the ALJ failed to consider the views of AHP's
expert witnesses regarding peripheral vascular disease. (AHP Exceptions
at 87-88.) AHP avers that its witnesses testified that the reanalysis
of the five-center study demonstrated a treatment effect. (AHP
Exceptions at 88, citing: Porter, A-109 at 22-25; Reichle, A-110 at 18-
20; Winsor at A-111 at 15-16; Reich, A-112 at 49-51.) As is apparent
from the ALJ's Initial Decision, the ALJ did consider AHP's evidence,
but the ALJ was not persuaded by it.
In any case, as I stated previously (see section I.C.1.c. of this
document), the Commissioner is not bound by the conclusions of expert
witnesses. (Warner-Lambert Co. v. Heckler, 787 F.2d at 154;
Commissioner's Decision on OPE, slip op. at 22; Commissioner's Decision
on Deprol, 58 FR 50929 at 50930.) Expert opinion testimony is only as
strong as the studies on which it is based. (Commissioner's Decision on
OPE, slip op. at 22, citing Upjohn v. Finch, 422 F.2d 944, 955 (1970).)
Having reviewed all of the evidence, I am in agreement with the
ALJ's conclusion that AHP did not provide a sufficient reason showing
that it was proper to analyze only the first 12 weeks
[[Page 64111]]
of this 24 week study. In a study such as the five-center study, where
major changes to the protocol were made but the decision to make those
changes was arrived at only after the data had been analyzed without
showing a statistically significant drug effect, it is not possible in
the subsequent reanalysis to ``distinguish the effect of a drug from
other influences, such as spontaneous change in the course of the
disease, placebo effect, or biased observation.'' (Sec. 314.126(a)) For
the above reasons, I therefore hold that AHP's reanalysis of the five-
center study can not be relied upon as substantial evidence of efficacy
from an adequate and well-controlled clinical trial.
b. Inclusion/exclusion decisions. As part of AHP's reanalysis of
the five-center study, Dr. Clarence Denton and Dr. Stuart L. Scheiner
reviewed the case reports for all of the 92 patients who completed the
first 12 weeks of the five-center study and reconsidered the inclusion/
exclusion decisions pertaining to each patient. (AHP Exceptions at 89;
A-108 at 2.) In their reanalysis, Drs. Denton and Scheiner were said to
have been blinded to such factors as whether a particular patient had
been included in the initial analysis, whether a patient had been on
drug or placebo, and as to a patient's outcome at the conclusion of the
five-center study. (AHP Exceptions at 89; AHP Post-Hearing Brief at 42;
Denton, Tr. Vol. VII at 10-11, 47.) However, it is not clear that Drs.
Denton and Scheiner were also blinded regarding the center to which a
patient had been assigned during the trial.
A total of 23 changes in the selection of patients for analysis
were made between the original analysis and the reanalysis. These
changes included 11 new inclusions and 11 new exclusions of patients,
and one reclassification of a patient who originally had been listed as
a placebo patient but upon discovery of a coding error was reclassified
as a Cyclospasmol patient. (I.D. at 27; A-108 at 11.) The ALJ
determined that these decisions were made post hoc and ruled that this
was another factor for which the reliability of the reanalysis can be
called into question. (I.D. at 56.) AHP disputes the ALJ's conclusions.
(AHP Exceptions at 88-98.)
The first objection raised by AHP on this point is to ask ``why''
the ALJ questioned the reliability of the 1985 five-center study. (AHP
Exceptions at 90-91.) This is a very broad and not well-defined issue,
but it appears that its gist is the argument that the ALJ did not
adequately explain the basis for his ruling on this issue. (AHP
Exceptions at 91.) I do not find this argument to be persuasive. The
ALJ devoted several pages of his decision to a discussion of the
reanalysis. (See I.D. at 26-31, 56.) In relevant part, the ALJ noted:
(1) That the five-center study was originally designed, conducted, and
analyzed with a crossover design, (2) that when the original analysis
failed to find a statistically significant drug effect, AHP sought to
rely upon the results from only one of the five centers, (3) that AHP
subsequently chose instead to reanalyze the first 12 weeks of the study
as if it had been a parallel study, (4) that in the reanalysis, the
inclusion and exclusion decisions for every patient were reconsidered
and 23 changes were made in patient selection, and (5) calculation of
the treadmill baseline data was not done in strict accordance with the
protocol, i.e., average values were used instead of the highest value.
(I.D. at 56.) As I ruled at the outset of this Final Decision, I find
that the ALJ's Initial Decision comports with the requirements of the
Administrative Procedure Act and FDA regulations, and that the ALJ
fully set out the reasons for his decision in the narrative explanation
section of his decision. (See section I.B. of this document.)
Therefore, I find no merit in AHP's argument.
AHP also challenges the ALJ's statement that the reanalysis should
be given a ``higher degree of scrutiny'' than the initial analysis.
(AHP Exceptions at 92-93.) As the ALJ stated in his opinion, ``(A)
higher degree of scrutiny is warranted here not because the reanalysis
was termed as such but because the reanalysis was undertaken in
response to the initial lack of a statistically significant difference
between the drug and placebo.'' (I.D. at 26.) The ALJ's statement was
appropriate, and I find no error in it.
AHP further argues that the ALJ misunderstood AHP's response to Dr.
Lipicky's ``accusations of manipulation.'' (AHP Exceptions at 93.) The
portion of Dr. Lipicky's testimony to which AHP refers reads as follows
regarding the reanalysis:
The first analysis showed that different investigators had
different results. If I had to search for a means of turning a
negative trial positive, I would retrospectively search for reasons
to exclude patients studied by investigators who did not produce
results favoring drug over placebo and include patients studied by
investigators who did favor drug over placebo. Remarkably, the
reanalysis, in addition to restricting attention to only \1/2\ of
the entire time of the study, excluded 7 patients from the Batson
study, 3 patients from the Raines study (both Batson and Raines
having not favored drug over placebo) and included 4 patients from
the Reich study (Reich having favored drug over placebo). Yet other
inclusions and exclusions resulted in a total of 20 patients (almost
25% of the patients analyzed) to be declared now analyzable whereas
previously being declared non-analyzable.
(Lipicky, G-61 at 18.)
AHP argues that Dr. Lipicky's testimony was refuted in AHP's Post-
Hearing Brief, wherein AHP had argued that ``(a)n examination of the
difference between the initial analysis and the reanalysis show that
AHP's inclusion/exclusion decisions in the reanalysis contradict(ed)
Dr. Lipicky's manipulation theory with respect to four of the centers;
only the Reich center was consistent with Dr. Lipicky's theory * * *.''
(AHP Post-Hearing Brief at 42 (emphasis in original).) The ALJ's
finding regarding this aspect of the reanalysis, with which AHP takes
issue, reads as follows:
In addition, AHP claims the Center's allegation is incorrect
with respect to four of the centers since patients were added, not
subtracted to the Raines center and excluded from the Batson-Hollier
and Abbott centers with no changes to the String center. Only the
Reich center showed a positive drug effect and had four patients
added to it.
(I.D. at 26-27.)
AHP now argues that in its Post-Hearing Brief, it had refuted Dr.
Lipicky's assertions in their entirety, and that the ALJ was in error
in finding that AHP had argued that the Center's allegation was
incorrect with respect to four of the five centers. (AHP Exceptions at
93.) I find this argument to be clearly without merit. As the
previously quoted excerpt from AHP's Post-Hearing Brief plainly shows,
AHP did say that it found that Dr. Lipicky's testimony was correct with
regard to the Reich center, just as the ALJ had ruled. (AHP Post-
Hearing Brief at 42.) I find no indication that the ALJ misunderstood
AHP's response to Dr. Lipicky's testimony, and, therefore, I find no
merit in AHP's argument.
AHP also argues that the ALJ was in error in stating that the Reich
Center was the only one of the five centers to show a ``positive drug
effect.'' (AHP Exceptions at 94.) In this statement, the ALJ was
referring to the initial analysis of the five-center study, in which
only the Reich Center showed a statistically significant drug effect.
(See I.D. at 26-27; G-9.1 at 85.) The ALJ also noted that when the
reanalysis was performed, four patients were added to the Reich Center.
(I.D. at 27.) The ALJ's statements were correct, and I find no error in
them.
AHP further challenges the ALJ's decision by asking what the ALJ's
rationale was for ruling that two patients who had been included in the
initial analysis--Patient Nos. 15 and 16
[[Page 64112]]
from the Batson-Hollier center--were improperly excluded from the
reanalysis. (AHP Exceptions at 94-98, citing I.D. at 28.) This issue
refers to the setting of a baseline treadmill measurement for patients
under a section of the protocol that has been termed the ``salvage''
provision. (AHP Exceptions at 95.) (Other issues related to the salvage
provision are discussed below in section I.C.2.c. of this document.)
Basically, the salvage provision was a contingency that required a
fairly stable treadmill measurement for the baseline for a patient's
entry into the study. Each patient entered into the five-center study
was enrolled in a 6 to 8 week, pretreatment washout period during which
all patients were given a placebo. (G-6 at 9.) A set of two treadmill
tests were performed each time a treadmill reading was required by the
study. (G-6 at 10.) To establish a patient's baseline value on the
treadmill, the maximum value recorded on the last visit of the
pretreatment period was to be used as the baseline. (G-6 at 10, 21.)
The protocol also provided that if the maximum values recorded on the
last two consecutive, pretreatment visits differed from one another by
more than 20 percent of the value of the larger of these two readings,
then up to two additional sets of treadmill tests at weekly intervals
could be made. (G-6 at 10-11.) Only the last two consecutive set of
tests would be considered for qualification of the patient into the
study. If agreement within 20 percent failed to be found after four
visits, the patient was to be dropped from the study. (G-6 at 11.)
In the initial analysis, Patient Nos. 15 and 16 from the Batson-
Hollier center were said to have entered the study under the salvage
provision, i.e., these patients required additional pretreatment visits
and treadmill tests to establish an acceptable baseline. (AHP
Exceptions at 95.) While these patients were included in the initial
analysis, these patients were excluded from the reanalysis. (AHP
Exceptions at 95.) Regarding this change in inclusion/exclusion
decisions, the ALJ wrote, ``AHP cannot exclude these patients after the
initial analysis failed to demonstrate a positive drug effect. There is
no reason why AHP could not have identified this problem area sooner.''
(I.D. at 28.)
I am in agreement with the ALJ's ruling on the exclusion of these
two patients. As I said before, inclusion/exclusion decisions made
after randomization may affect the initial randomization and assignment
of subjects in such a way as to bias the results. (Commissioner's
Decision on OPE, slip op. at 238-39; Commissioner's Decision on Deprol,
58 FR 50929 at 50939 and 50940.) In the present case, the issue of bias
has been raised all the more strongly because the exclusions also
involved a change in the protocol and subsequent reanalysis after the
initial analysis failed to find statistical significance. I find AHP's
exclusion of these patients effectively to be a change in the entry
criteria made after the data were collected, analyzed, and failed to
show statistically significant results. The ALJ was right to question
it. Therefore, I uphold the ALJ's rejection of the inclusion/exclusion
decision regarding these two patients in the reanalysis.
AHP further argues that the ALJ misunderstood AHP's evidence
regarding the exclusion of Patient Nos. 15 and 16 from the Batson-
Hollier center. (AHP Exceptions at 98.) On this point, AHP takes issue
with the following statement by the ALJ: ``This (exclusion of patients
who would have qualified for entry in the study by means of the
`salvage provision'), according to AHP, explains why the patient
population at the Batson-Hollier Center was different than that of the
other centers.'' (I.D. at 28; see AHP Exceptions at 98.) I have
reviewed the record, and I find that the ALJ's opinion accurately
summarizes the statements made by AHP in its Post-Hearing Brief,
particularly this language from that brief: ``The patient population
studied at the one center (the Batson center) was, as a consequence (of
the salvage provision), different from the patient population studied
in the other four centers.'' (AHP Post-Hearing Brief at 52.) Therefore,
I find no merit in AHP's argument.
I am in agreement with the ALJ's determination that the inclusion/
exclusion decisions called the reliability of the reanalysis into
question. An adequate and well-controlled study must ensure that
adequate measures are taken to minimize bias on the part of the
analysts. (Sec. 314.126(b)(5)) Exclusion decisions made after
randomization may affect the initial randomization and the assignment
of subjects in such a way as to bias the results. (Commissioner's
Decision on OPE, slip op. at 238-39; Commissioner's Decision on Deprol,
58 FR 50929 at 50939-40.) Under the facts in the present case, it is
not possible in the reanalysis to distinguish the effect of a drug from
other influences, such as biased observation. (See Sec. 314.126(a).)
Therefore, for the reasons previously discussed I reject AHP's
exceptions.
c. Calculation of treadmill distances. As previously indicated,
each patient entered into the five-center study was enrolled in a 6 to
8 week, pretreatment washout period during which all patients were
given a placebo. (G-6 at 9.) As provided under the protocol, a set of
two treadmill tests were to be performed each time a treadmill reading
was required by the study. (G-6 at 10.) To establish the baseline value
for a patient on the treadmill, the maximum value recorded on the last
visit of the pretreatment period was to be used as the baseline. (G-6
at 10, 21.) The protocol also stipulated that if the maximum values
recorded on the last two consecutive pretreatment visits differed from
one another by more than 20 percent of the larger of these two values,
then, under a section of the protocol referred to as the ``salvage
provision'' (AHP Exceptions at 95), up to two additional sets of
treadmill tests at weekly intervals could be made. (G-6 at 10-11.) Only
the last two consecutive sets of tests would be considered for
qualification of the patient into the study. If agreement within 20
percent failed to be found after four visits, the patient was to be
dropped from the study. (G-6 at 11.) The protocol contained a
comparable requirement for the measurement of treadmill values
throughout the study, in that ``(t)he test resulting in the longer
claudication time (was to) be used for calculating the maximum distance
walked.'' (G-6 at 21 (emphasis in original).)
The report of the initial analysis for the five center study stated
that ``the baseline measurement used was the maximum of the two values
from the last visit'' of the pretreatment period. (G-9.1 at 90.)
However, it is not clear that, in fact, the maximum values were used
for all five of the centers, for in a separate report on the MDS-176
(Reich) center it was stated that the baseline measurement was ``the
average of the last two visits of the single blind pre-medication
placebo phase'' (G-9.1 at 180 (emphasis added)), rather than the
maximum value as provided in the protocol. Moreover, in the reanalysis,
AHP calculated the baseline values for each patient by averaging the
two treadmill measurements from the pretreatment results rather than by
using the maximum value, as per the protocol. (Lipicky, Tr. Vol. IV at
70; see also A-108 at 2-11; AHP Exceptions at 100.)
In his Initial Decision, the ALJ found, ``AHP also did not
calculate all the treadmill data in strict accordance with the
instruction of the protocol.'' (I.D. at 56.) AHP takes exceptions to
the ALJ's findings on this point. (AHP Exceptions at 98.) AHP first
avers that no witness
[[Page 64113]]
for the Center criticized the 1985 five-center study analysis on the
basis of the manner in which the baseline treadmill values for patients
were calculated, and that the issue was raised for the first time by
the Center in its brief. (AHP Exceptions at 101.) However, my review of
the hearing transcript reveals that Dr. Lipicky, a witness for the
Center, testified, ``(E)ven though the protocol clearly stated that the
analysis was to be based upon the longest walking distance measured at
any of the visits, AHP chose to use mean values of the two treadmill
walking times that were measured at each visit.'' (Lipicky, Tr. Vol. IV
at 70.) The calculation of treadmill values was identified as a
protocol violation by the Center at the hearing, and so AHP's
assertions to the contrary are simply incorrect.
AHP next argues that the Center, in preparing its own analysis of
the data, computed baseline and final treadmill measurement by
averaging the measurements from the study. (AHP Exceptions at 102-03.)
In support of its argument, AHP cites to the testimony of Dr. Lipicky,
a witness for the Center, who relied upon an exhibit identified as G-70
in his testimony on this point. (See Lipicky, Tr. Vol. IV at 74-82, 97-
104.)
The record indicates that the Center performed at least eight
different analyses in its review of the five-center study, with exhibit
G-70 being one of the Center's analyses. (Lipicky, Tr. Vol. IV at 75.)
Dr. Lipicky testified that in Exhibit G-70, the Center looked at the
data in the same way as did AHP in its reanalysis. (Lipicky, Tr. Vol.
IV at 76.) Baseline walking distances were computed by averaging a
given patient's test measurements at the third and fourth visits.
(Lipicky, Tr. Vol. IV at 98.) However, I note that Exhibit G-70 was
stricken from evidence by the ALJ on motion of AHP. (Tr. Vol. V at 6.)
Therefore, I find any issues pertaining to Dr. Lipicky's testimony
regarding this evidence to be moot.
AHP also asks if the ALJ considered whether the study results would
have been any different if maximum values had been used rather than
average values. (AHP Exceptions at 103.) The ALJ is not required to
perform such calculations. More importantly, the fact is that AHP's
calculation of the treadmill values using average values was yet one
more protocol violation in a study with other protocol violations.
AHP raises the additional argument that the ALJ rejected the five-
center study solely on the basis of AHP's use of average treadmill
values instead of the maximum values required by the protocol. (AHP
Exceptions at 103.) This is a misstatement of the ALJ's opinion. The
ALJ rejected the reanalysis because AHP ``provided no good reason'' for
analyzing only the first half of the data from this study. (I.D. at 30)
Therefore, I find AHP's argument to have no merit.
d. Variability among centers. AHP next objects to the ALJ's ruling
that the results of the various centers within the five-center study
are so inconsistent as to make any finding of a significant drug effect
questionable. (AHP Exceptions at 105, citing I.D. at 31.) In its
arguments, AHP raises the broad questions of when it is appropriate to
``break open'' a multicenter study and review the results of individual
centers, and what it is that the ALJ should examine in such a review.
(AHP Exceptions at 107-08.)
By statutory mandate, FDA is charged with reviewing all DESI drugs
for efficacy and to withdraw approval for any NDA where ``substantial
evidence'' of the drug's effectiveness is lacking (21 U.S.C.
355(e)(3)). Among the considerations to be weighed in the FDA's review
are the validity of the methodology used in a particular study, and the
determination of whether substantial evidence of efficacy has been
proved. (Warner-Lambert, 787 F.2d at 153.)
To this end, a thorough review of the studies submitted by a
manufacturer to the FDA as proof of a drug's efficacy is always
appropriate. All aspects of the data are proper subjects for review.
When the study is a multicenter trial, the methodology and data from
each participating center may be evaluated and reviewed. I therefore
find that the ALJ did not err when he ``broke open'' the multicenter
trial and reviewed the outcome at each of the centers.
AHP next argues that the ALJ ignored the pooled results of the
five-center study. (AHP Exceptions at 107.) I find that the ALJ did
weigh the pooled data but that he concluded that the data failed to
meet the requirements of an adequate and well-controlled study. (See
generally Commissioner's Decision on Phenformin Hydrochloride (44 FR
20967 at 20970, April 6, 1979) (Commissioner ruled that ALJ did not
disregard specified evidence but instead was found to have considered
the overall evidence.))
AHP next challenges the ALJ's finding that ``the results of the
five-center study are so inconsistent as to make a significant drug
effect questionable.'' (AHP Exceptions at 105, quoting I.D. at 31.) I
find that the ALJ's ruling is supported by the evidence. Regarding the
reanalysis, Dr. Schneiderman, a witness for the Center, testified that
there were substantial differences among the five centers in the study.
(Schneiderman, Tr. Vol. VII at 8.) On this point, Dr. Schneiderman
testified:
Oh, I think there's a substantial difference among the
institutions that tested the patients. One institution shows
substantial improvements in the average among the patients, much of
that improvement being contributed by one patient who was in one of
the inclusions--included once and excluded once--thereby, the
selection criteria become of considerable importance in that one
institution.
In the four other institutions, two of them show some minor effects
for the drug, slightly better than placebo; two of them show some minor
effects for placebo, slightly better than the drug. So it seems to me
there was a substantial difference among the institutions.
(Schneiderman, Tr. Vol. VII at 8.)
Additionally, another Center witness, Dr. Lipicky, testified that
results of the various investigators differed to an extent that made
the pooled data difficult to accept as accurate. (Lipicky, G-61 at 19.)
Dr. Lipicky reported that two of the five centers found the placebo to
be numerically superior to Cyclospasmol, and that it was the
Reich Center which found the largest numerical difference between drug
and placebo. Dr. Lipicky further testified, ``Within the study,
replication is poor and this remains a major problem. In fact at one
point in time AHP used this argument to argue the results of the
multicenter study could not be pooled.'' (Lipicky, G-61 at 19.)
e. Adequacy of the five-center study. In sum, I find that the five-
center study was not adequate and well-controlled. In making this
determination, I have considered the aggregate effect of the protocol
violations. As I previously discussed: (1) AHP's reanalysis of the
five-center study cannot be relied upon as substantial evidence of
efficacy from an adequate and well-controlled clinical trial; (2)
reconsideration of the inclusion/exclusion decisions called into
question the reliability of the reanalysis; (3) calculation of
treadmill distances were not performed according to the protocol; and
(4) the evidence indicated that results of the various centers differed
to an extent that made the pooled data difficult to accept as accurate.
D. The Senile Dementia Disease Indication
The labeling for Cyclospasmol originally identified
``selected cases of ischemic cerebral-vascular disease,'' as being one
of Cyclospasmol's indications. (G-33.2 at 7; see also A-89 at
4-6; G-57 at 4-7.) However, AHP has modified this proposed labeled
indication to that of treatment for cognitive dysfunction in patients
[[Page 64114]]
suffering from senile dementia of the multiinfarct or Alzheimer's type.
(See AHP Post-Hearing Brief at 1; AHP Exceptions at 111.)
Senile dementia is a clinical term used to describe a series of
conditions in which elderly individuals have memory loss and cognitive
impairment. (Thal, G-63 at 3.) There are various etiologies which can
result in the clinical syndrome of senile dementia. (Thal, G-63 at 3.)
Multiinfarcts and Alzheimer's disease are two such etiologies. Other
diseases and conditions which can cause dementia include psychiatric
problems masquerading as dementia, metabolic disorders, such as
hyperthyroidism or Vitamin B-12 deficiency, diseases of the central
nervous system, and systemic illnesses that affect the function of the
central nervous system, such as diseases of the heart, lungs, liver,
kidneys, endocrine and hematologic organ systems. (Thal, G-63 at 3;
Leber, G-64 at 5.)
Cognitive dysfunction is a symptom of senile dementia. (Zung, Tr.
Vol. III at 43.) Cognitive dysfunction can include a lack of mental
alertness, confusion, inattentiveness, memory problems, and
disorientation. (Goodman, A-123 at 4; Klerman, A-118 at 6.) Emotional
or motivational disturbances are also sometimes associated with
cognitive dysfunction. (Klerman, A-118 at 7.)
AHP submitted two studies in support of the dementia indication--
the Rao study and the Yesavage study. Each study will be reviewed in
turn.
1. The Rao Study
The Rao study was a placebo-controlled, parallel group study
conducted from December 1975 through June 1976 at Oak Forest Hospital,
Illinois, by Drs. Dodda B. Rao, Emile L. Georgiev, P.D. Paul, and A.B.
Guzman. (I.D. at 32.) The stated objective of the study was ``to
evaluate the efficacy of Cyclospasmol in alleviating symptoms
of senescence commonly associated with cerebral vascular
insufficiency.'' (G-28.8 at 314.)
Patients in the drug group were given 1,600 mg of
Cyclospasmol per day for 12 weeks, while patients in the
control group received a placebo. (G-28.8 at 314.) Seventy patients
were enrolled in the study. However, nine patients dropped out and
three patients were later excluded from the statistical analysis,
leaving 58 patients whose results were included in the final analysis.
(I.D. at 32.)
Patients in the Rao study were rated by using the Sandoz Clinical
Assessment--Geriatric (SCAG), and the Nurses Observation Scale--
Inpatient Evaluation (NOSIE). (G-14.2 at 242-43.) Also, a global
evaluation of each patient's clinical improvement was made at final
visit. (G-14.2 at 243-44.)
With the SCAG measurement, a physician rated each patient based on
a list of 19 items, or symptoms, associated with dementia. (G-3.1 at
97.) These items included attributes such as ``confusion,''
``bothersomeness,'' ``appetite,'' and ``anxiety.'' (G-3.1 at 98.) Each
Item in the SCAG was rated on a scale from 1 to 7, with 1 indicating
that the symptom was ``not present,'' and 7 indicating that the symptom
was ``severe.'' (G-3.1 at 97; see, e.g., G-14.2 at 6-8.)
Eighteen of the SCAG items were then grouped into five factors for
patient rating. (G-3.1 at 97; see also G-11.1 at 69-71 (Dr. Yesavage
discussing SCAG in the Yesavage study).) The five factors for the SCAG
included: (1) Cognitive dysfunction, (2) interpersonal relationships,
(3) affect, (4) apathy, and (5) somatic dysfunction. The 19th item, a
physician's overall assessment of the patient, was rated separately and
was not grouped into a factor. (G-3.1 at 97; see also G-11.1 at 70 n.7
(Dr. Yesavage discussing SCAG in the Yesavage study).)
The NOSIE rated the frequency of 30 specific behaviors, employing a
scale from ``1'' for ``never,'' to ``5'' for ``always.'' (See, e.g., G-
14.2 at 10.) Among the rated behaviors were such items as ``is
sloppy,'' ``sleeps, unless directed into activity,'' and ``has trouble
remembering.'' (See, e.g., G-14.2 at 10.)
For the final, global evaluation, the patient's physician rated the
patient's overall clinical condition during the study as being either
``worsened,'' ``unchanged,'' ``minimal improvement,'' ``moderate
improvement,'' or ``marked improvement.'' (See, e.g., 14.2 at 25.)
Regarding the SCAG ratings, Dr. Rao reported a statistically
significant change from baseline in favor of Cyclospasmol on
four of the five SCAG Factors, but not on the separate SCAG Item 19.
(G-3.1 at 97-98.)
As for the NOSIE results, the Rao study grouped the 30 items on the
NOSIE into 5 factors, identified as: (1) Social competence, (2) social
interest, (3) personal neatness, (4) irritability, and (5) retardation.
(G-3.1 at 98.) The specific grouping into factors was not discussed in
the report on the Rao study. (See G-3.1 at 96-99.) However, it was
reported that for three of the five NOSIE factors, the test and control
arms were not comparable at baseline. (G-3.1 at 98.) For the remaining
two NOSIE factors, which were found to have been comparable at
baseline, it was reported that statistical significance was not shown
for Cyclospasmol. (G-3.1 at 98.)
As for the physicians' global evaluations, Dr. Rao reported a
statistically significant difference in favor of
Cyclospasmol. (G-3.1 at 98, 99.)
The ALJ ruled that the Rao study cannot be considered an adequate
and well-controlled study because he found that the study was conducted
``so poorly that the results cannot be relied on with any degree of
certainty.'' (I.D. at 42.) Both AHP and the Center raise objections
pertaining to rulings made by the ALJ regarding the Rao study.
a. Admissibility of the reanalysis. AHP argues that the ALJ erred
in refusing to admit AHP's reanalysis of the Rao study into evidence.
(AHP Exceptions at 117-21; I.D. at 9.) In denying the admission of the
reanalysis into evidence, the ALJ ruled that the reanalysis was not
timely filed as required under FDA regulations. (I.D. at 9; ALJ Order
of 5/29/85, Exhibit Vol. 89; Sec. 12.85 (21 CFR 12.85.)) The ALJ
further ruled that AHP failed to demonstrate, as was required per the
regulations, that AHP could not have submitted the reanalysis sooner,
and that the value of the reanalysis to the evidentiary record would
justify potential delay resulting from the document's late submission.
(I.D. at 9; see Sec. 12.85(c).)
The circumstances preceding the submission of the reanalysis are
not in dispute. Following the publication in the Federal Register on
May 25, 1979, of a Notice of an Opportunity for a Hearing regarding
Cyclospasmol (44 FR 30443), AHP made a request for a hearing
and submitted in support of Cyclospasmol's efficacy a four
page article published by Dr. Dodda B. Rao discussing this study.
(Center Exceptions at 34.) Subsequently, FDA asked AHP for the Rao
study's case report forms, but AHP advised FDA that only 3 of the 58
forms could be located. (Center's Narrative, G-57 at 5.) In July of
1984, representatives of FDA visited Oak Forest Hospital and were able
to locate and review the hospital records for 56 of the 58 subjects in
the Rao study. (Center Exceptions at 35, citing Center's Allegations of
Fact Nos. 58-62; Center's Narrative, G-57 at 5.)
In October of 1984, the Center filed its Narrative Statement in
which the Center criticized the Rao study for failing to exclude
certain patients who had been given concomitant medications during the
study and for other violations of the protocol's exclusionary
requirements. (Center Exceptions at 35; see Center's Narrative, G-57 at
1-8.) On December 17, 1984, AHP filed with the administrative record
copies of AHP's
[[Page 64115]]
documentary data and other information relied upon, as required under
FDA regulations. (Sec. 12.85.) The reanalysis of the Rao study was not
included with AHP's prehearing submission.
On May 6, 1985, a reanalysis of the Rao study was submitted as an
attachment to the deposition testimony of Mr. Danny Chaing. (A-125,
Attachment E.) In this reanalysis, AHP excluded 14 patients from the
analysis because of concomitant medication violations or concomitant
diseases and conditions. (AHP Exceptions at 118.) The results of the
reanalysis, using 44 patients of the 58 patients originally analyzed,
were reported as showing statistical significance in favor of
Cyclospasmol. (AHP Exceptions at 119.)
The Center moved to strike the reanalysis on the grounds that it
was a late submission and that there was no justification for its
delayed filing. (Center Motion to Strike 5/13/85, Exhibit Vol. 88 at p.
12-13.) The Center argued that the reanalysis should have been
submitted to the FDA in either the NDA for Cyclospasmol or in
the prehearing submissions required under FDA regulations.
(Sec. 12.85.)
FDA regulations require that within 60 days of the publication of
the notice of hearing, each participant in the hearing shall submit to
the docket all data and information relied upon. (Sec. 12.85(b).) The
regulations further provide that such submissions may be supplemented
later in the proceeding, with the approval of the presiding officer,
upon a showing that the material contained in the supplement ``was not
reasonably known or available when the submission was made or that the
relevance of the material contained in the supplement could not
reasonably have been foreseen.'' (Sec. 12.85(c).)
If written evidence is not submitted as required under the
regulations, the ALJ may exclude the evidence as inadmissible.
(Sec. 12.94 (21 CFR 12.94(c)(1)(iii)).) Under the regulations, the ALJ
in the present case excluded the Rao reanalysis, inasmuch as the
submission was neither timely filed, nor was a motion to supplement
AHP's submissions made offering an explanation for the lateness of the
submission.
In support of its submission, AHP argues that the reanalysis was
``highly relevant,'' and that the reanalysis was the appropriate
response to the Center's criticisms of the Rao study. (AHP Exceptions
at 120.) AHP also argues that the ALJ's ruling prevented AHP from
demonstrating that even if certain patients were excluded from the
statistical analysis, the Rao study still resulted in a statistically
significant result. (AHP Exceptions at 121.) I find that these
arguments merely beg the question and do not address the fact that AHP
made no attempt to offer a motion with explanation to the ALJ to
supplement AHP's submissions for the Rao study, as stipulated in the
regulations. (Secs. 12.85(c) and 12.94(c)(1)(iii).) (By contrast, I
note that AHP made such a motion, which was granted by the ALJ, to
supplement its submissions in connection with the five-center study.
(See I.D. at 8-9.))
The reanalysis submitted by AHP entailed a reconsideration of the
exclusionary decisions made regarding the study subjects and a
recalculation of statistical significance. As was ruled in the
Commissioner's Decision on the drug Cothyrobal, ``(I)t is not the
function of a hearing to consider new evidence, i.e., evidence that was
not available to the agency at the time it initially denied the NDA.''
(Commissioner's Decision on Cothyrobal, 42 FR 28602 at 28616, June 3,
1977), aff'd Edison Pharmaceutical Co. v. FDA, 600 F.2d 831 (1979); see
also Warner-Lambert, 787 F.2d at 162 (ALJ has ``the power to make
reasonable, nonarbitrary decision regarding the admission or exclusion
of evidence for procedural reasons.'').)
Similar decisions pertaining to administrative hearings before
other Federal agencies have been affirmed by the courts. For example,
in Michigan Consolidated Gas Co. v. Federal Energy Regulatory Comm'n,
883 F.2d 117, 124-25 (D.C. Cir. 1989), the circuit court ruled, ``When
a party is on reasonable notice as to the dates and times for hearings
and for filings in an administrative proceeding, we are hard pressed to
hold that the administering agency acted arbitrarily or capriciously in
denying admission of materials untimely filed.'' (See also Irving Bank
Corp. v. Board of Governors of Fed. Reserve System, 845 F.2d 1035, 1039
n.5 (1988) (Board of Governors of Federal Reserve System had discretion
over extent to which it was required to consider late-submitted
evidence); Pittsburgh & Lake Erie R.R. Co. v. Interstate Commerce
Comm'n, 796 F.2d 1534, 1544-45 (D.C. Cir. 1986) (Carrier challenging
cancellation of several joint rates was not entitled to admission of
certain rebuttal evidence which the carrier submitted at a stage in the
administrative proceedings when the opposing party would not have had
an opportunity to respond.))
In challenging an evidentiary ruling such as this, the objecting
party has the burden to make a ``strong showing'' that the ALJ abused
his or her discretion. (Warner-Lambert, 787 F.2d at 162.) I do not find
that AHP has made the necessary strong showing that such an abuse of
discretion occurred on the part of the ALJ. Therefore, I find that the
ALJ did not err in granting the Center's motion to strike the
reanalysis.
b. Labeling and patient selection. AHP next argues that the ALJ
erred in concluding that the Rao study was not adequate and well-
controlled because the claimed indications for Cyclospasmol
went beyond those of the patient group which was originally said to
have been studied. (AHP Exceptions at 121; I.D. at 34, 42, 56.) The ALJ
had noted that while AHP was now seeking to label
Cyclospasmol for indications in patients with dementia
resulting from both Alzheimer's disease and from multiinfarcts, Dr.
Rao, in his published account of the study, stated that he had excluded
patients with ``a history of Alzheimer's disease.'' (I.D. at 56; G-3.1
at 97.)
As stated in the protocol, the objective of the Rao study was ``to
evaluate the efficacy of Cyclospasmol in alleviating symptoms
of senescence commonly associated with cerebral vascular
insufficiency.'' (G-28.8 at 314.) The protocol also required, among
other things, that patients ``whose symptoms of senescence occurred
prior to age fifty'' be excluded. (G-28.8 at 314.)
Dr. Rao, in his subsequently published article, indicated that the
focus of the study was the treatment of cerebrovascular insufficiency.
(G-3.1 at 96.) Dr. Rao noted ``that in the past vasodilators have too
often been prescribed indiscriminately, without proper selection of
patients.'' (G-3.1 at 97.) Dr. Rao then went on to describe the patient
population for his study as follows:
Sixty geriatric patients (men and women aged 65 or older) were
selected initially for the study. We excluded those with a history
of Alzheimer's disease; stroke; psychiatric illness; traumatic,
neoplastic or infective brain damage; and other relevant disorders.
We attempted to identify patients with clearly evident symptoms of
senility, but excluded those who were so severely debilitated as to
make the possibility of significant improvement unlikely.
(G-3.1 at 97.)
Notwithstanding Dr. Rao's article reporting that he had excluded
patients with Alzheimer's disease, AHP argues that Dr. Rao's exclusions
did not prevent the study population from including patients with
dementia due to Alzheimer's disease. (AHP Exceptions at 123.) AHP
argues that the definition of Alzheimer's disease has changed since the
time of Dr. Rao's article. AHP argues that in the mid-1970's, when Dr.
Rao conducted this study and published his
[[Page 64116]]
article, Alzheimer's disease was defined as dementia in a relatively
young patient population, i.e., patients under age 65. Dr. Rao, when he
purported to be excluding Alzheimer's patients from his study, excluded
only dementia patients under age 65. This definition for Alzheimer's
disease is today outmoded. (AHP Exceptions at 122; Zung, Tr. Vol. III
at 15-16.) AHP argues that today the definition of Alzheimer's disease
includes patients over the age of 65, which would include patients in
the age group represented in the Rao study.
Citing the change in the definition of Alzheimer's disease, AHP
also argues that despite Dr. Rao's claim of excluding Alzheimer's
disease patients from the study, Dr. Rao could not possibly have
excluded patients with Alzheimer's disease because the only way to
differentiate conclusively between multiinfarct dementia and
Alzheimer's disease is by an autopsy. (AHP Exceptions at 123, citing
Denton, Tr. Vol. VII at 14; Yesavage, Tr. Vol. IV at 27; Yesavage, A-
115 at 7.) AHP argues that the patient population represented in the
Rao study was the same as would currently be identified as suffering
from either multiinfarct dementia or Alzheimer's disease. (AHP
Exceptions at 123.) AHP concludes by arguing that Dr. Rao's exclusions
did not prevent the Rao study population from including patients with
both multiinfarct dementia and dementia due to Alzheimer's disease,
notwithstanding Dr. Rao's contrary intention. (AHP Exceptions at 123.)
AHP cites to the testimony of three witnesses in support of its
position. (AHP Exceptions at 123.)
The first of the witnesses cited by AHP is Dr. Lowell I. Goodman, a
witness for AHP, who testified generally about the population suffering
from dementia. Dr. Goodman stated, ``Almost certainly subsequent
epidemiological studies and further research into this population have
revealed that approximately two-thirds of such patients, diagnosed as
having senile dementia, were of the Alzheimer type and approximately a
third were either multiinfarct dementia or a mixture of the two.''
(Goodman, Tr. Vol. V at 82.)
AHP also cited to the testimony of Dr. Gerald L. Klerman, also an
AHP witness, who testified:
Our current thinking is that cerebral arteriosclerosis plays
relatively little role in most cases of senile dementia and that
they are either of the Alzheimer's type or what is called multi-
infarct dementia. The Rao and the Yesavage study by current
standards would be primarily cases with Alzheimer's disorder and
some with a mixture of previous strokes.
(Klerman, Tr. Vol. III at 69.)
The third witness cited by AHP is Dr. Leon J. Thal, a witness for
the Center. I have reviewed Dr. Thal's testimony, however, and I do not
find it to support the point being advanced by AHP. When Dr. Thal was
asked whether it was likely that the patient population chosen under
the Rao protocol, i.e., patients having ``symptoms of senescence
commonly associated with cerebral vascular insufficiency,'' would today
be the same as a population consisting of Alzheimer's patients and
multiinfarcts dementia patients, Dr. Thal responded in the negative.
Contrary to the position which AHP is arguing, Dr. Thal testified,
``No, that's not correct because, in addition to multi-infarct dementia
and Alzheimer's disease, there are many other causes of dementia. The
patients in the Rao study were not systematically examined for other
causes of dementia.'' (Thal, Tr. Vol. VI at 38.) Dr. Thal went on to
add that even if Alzheimer's disease patients and multiinfarct patients
were counted as one group, still it was likely that approximately 20
percent of the patients included in the Rao study had other causes of
dementia. (Thal, Tr. Vol. VI at 38.)
FDA regulations require that ``(t)he method of selection of
subjects provides adequate assurance that they have the disease or
condition being studied * * *.'' (Sec. 314.126(b)(3).) Towards this
end, the Commissioner's Decision on Mysteclin, relying upon this
section of the regulations, stated:
It is essential, therefore, that the most accurate diagnostic
techniques available be used in order to provide as much assurance
as possible that the results are credible. See Lutrexin; Withdrawal
of Approval of New Drug Application, 41 Fed. Reg. 14406, 14419
(1976). Because patients often are treated on the basis of
preliminary diagnoses that suggest, without confirmation, a
disease's etiology, the diagnostic criteria used by physicians when
treating patients are not always applicable in the context of a drug
investigation.
(Commissioner's Decision on Mysteclin, slip op. at 36-37, FDA Docket
No. 82N-0153 (FDA February 8, 1988) (some citations omitted), opinion
denying review sub nom. E.R. Squibb & Sons, Inc., v. Bowen, 870 F.2d
678 (D.C. Cir. 1989) (hereinafter cited as Commissioner's Decision on
Mysteclin).)
Leaving aside the question of Dr. Rao's intent, I turn instead to
the evidence that Alzheimer's and/or multiinfarct patients were
included in the Rao study, and that patients with other causes of
dementia were excluded. The evidence argued by AHP basically consists
of the facts that: (1) The patients in the study exhibited dementia,
and (2) the patients were in the typical age group for patients having
Alzheimer's or multiinfarct.
I find that evidence about dementia in general in the geriatric
population, such as that evidence offered by Drs. Goodman and Klerman,
does not provide adequate assurance that the subjects of the Rao study
had Alzheimer's disease. As Dr. Thal, the third witness cited by AHP,
testified, dementia can be caused by various conditions or diseases.
(Thal, Tr. Vol. VI at 38.) Included among these other diseases or
conditions are hypothyroidism, vitamin B12 deficiency,
hydrocephalus, psychiatric problems (pseudodementia), chronic
alcoholism, Parkinson's disease, severe diabetes, neurological disease,
infection in the central nervous system, and brain tumors. (Zung, Tr.
Vol. III at 17-18; 23-24, 32, 50; Goodman, Tr. Vol. V at 82-83;
Goodman, A-123 at 23.) Despite this fact, the evidence does not show
that the patients in the Rao study were examined for other causes of
dementia. (Thal, Tr. Vol. VI at 38.)
AHP argues that it did perform a physical examination to screen for
other neurological causes of dementia. (AHP Post- Hearing Brief at 88;
see Goodman, A-123 at 21-23; Goodman, Tr. Vol. V at 82-83; Zung, A-117
at 30.) This examination was said to consist of an evaluation of each
patient's gait, muscle strength, balance, deep-tendon reflexes, level
of consciousness, attention and understanding, cooperation and
intelligence, and visual, auditory and other special senses. (Goodman,
A-123 at 21.) However, none of the results of these tests were in
evidence, nor were the results available for review by the Center. In
the absence of evidence of the results of such tests, AHP's argument
that it did perform certain diagnostic tests is not persuasive and has
no probative value. (Commissioner's Decision on Cothyrobal, 42 FR 28602
at 28608 (Where a particular condition can be caused by many factors,
evidence must be provided regarding diagnostic criteria and the
confirmatory laboratory tests.))
AHP further argues that, because most of the patients entered into
the study had been under the close supervision of the study's
physicians for years and were familiar to the physicians before the
study began, further diagnostic testing was not necessary to screen for
other causes of dementia. (AHP Post- Hearing Brief at 88; see Klerman.
A-118 at 28-29; Goodman, A-123 at 21-23; Goodman, Tr. Vol. V at 82-83;
Zung, A-117 at 30.) I am not persuaded by this argument. By statutory
mandate, a
[[Page 64117]]
drug's efficacy must be proved by substantial evidence from adequate
and well-controlled clinical trials. (21 U.S.C. 355(d).) It is
established that the burden of proving the adequacy of a study is on
the proponent for the drug. (Hynson, 412 U.S. at 617, citing 21 U.S.C.
355(e)(3).) Under agency regulations, the method of selecting subjects
for a study must provide adequate assurance that the subjects have the
disease or condition being studied. (Sec. 314.126(3).) In the Rao
study, I do not find the undocumented, prestudy experience of the
physicians with the study patients to be acceptable as substantial
evidence of the patients' conditions.
As for the change in the definition of Alzheimer's disease, I find
this equally unpersuasive as a basis for supporting an indication for
Alzheimer's disease. As I previously stated, general observations about
the geriatric, senile population at large do not provide adequate
assurance that the subjects of the Rao study had Alzheimer's disease.
Moreover, as AHP concedes, Alzheimer's disease and multiinfarct
dementia are distinct diseases with different etiologies. AHP argues
that etiology does not matter because AHP does not have to prove the
mechanism of action for Cyclospasmol. While it is true that
the regulations do not require proof of mechanism of action, this is
beside the point now at issue. The issue is diagnosis of the disease,
not mechanism of action for the drug. In an adequate and well-
controlled study, it is not acceptable to group persons having similar
symptoms but distinct diseases together into one study without
identifying which patient has which disease (as was done in the Rao
study). If this practice were permitted, it would be impossible to
assess a drug's effectiveness on a particular disease. (Cf.
Commissioner's Decision on Lutrexin, 41 FR 14406 at 14422 (In a study
of premature labor, results were incapable of scientific interpretation
because patients with different conditions were evaluated together
without distinguishing between the conditions.); see also
Commissioner's Decision on Cothyrobal, 42 FR 28602 at 28608 (Where a
particular condition can be caused by many factors, evidence must be
provided regarding diagnostic criteria and the confirmatory laboratory
tests.))
Difficulty in diagnosis is not a justification for a less than
adequate and well-controlled study. (Commissioner's Decision on
Cothyrobal, 42 FR 28602 at 28608.) While Alzheimer's disease may not be
positively diagnosed until an autopsy is performed, evidence indicated
that it was possible to make a differential diagnosis on the basis of
patient history by ruling out other causes of dementia. On this point,
Dr. William Zung, a witness for AHP, testified that in order to make a
differential diagnosis, one must consider the history of the patient.
Dr. Zung testified that with Alzheimer's disease, ``the signs and
symptoms are progressive. They are of a slow onset.'' (Zung, Tr. Vol.
III at 14.) However, for multiinfarct dementia, Dr. Zung testified,
``the symptomatology would come on fairly rapidly * * *.'' (Zung, Tr.
Vol. III at 14.) Dr. Zung further testified:
(Y)ou can tell a differential diagnosis between senile dementia
of the Alzheimer type and the multi-infarct because patients who
have multi-infarct dementia have focal signs. That is to say,
specifically where that part of the brain has been affected by lack
of the oxygen and by death of the cells, say, if it's in the motor
part of the brain, then that patient would have a decrease in their
motor function.
(Zung, Tr. Vol. III at 15.)
I find that for an adequate and well-controlled study, merely
selecting an elderly population which has dementia is not sufficient to
assure that the study will demonstrate the effectiveness of a drug for
patients with Alzheimer's disease. While the ``gold standard'' for
diagnosing Alzheimer's disease lies in autopsies, nonetheless, there
was evidence indicating that antemortem diagnosis can be made by the
process of eliminating other possible causes of dementia.
Identification of dementia caused by other conditions must be made and
patients with other causes for their dementia excluded from the study.
Alternatively, if patients with other causes of dementia, such as
multiinfarct dementia, are to be included, then all patients' diagnoses
should be identified.4
---------------------------------------------------------------------------
\4\ I note that this was done in the Yesavage study. (See
Yesavage, Tr. Vol. IV at 27.)
---------------------------------------------------------------------------
As was ruled in the Commissioner's Decision on Lutrexin, ``The
evidence made clear that although existing diagnostic techniques do not
permit certainty in the matter, they do allow physicians to make a
valid judgment * * *. That the judgment will sometimes prove to be
incorrect does not mean that diagnosis * * * is impossible, only that
it is inherently uncertain.'' (41 FR 14406 at 14414.) Similarly, in the
Commissioner's Decision on Cothyrobal, it was ruled that where a
disease or condition can be caused by many factors, a study must give
the patients' diagnoses and must also provide sufficient information to
substantiate the diagnoses, notwithstanding the fact that a particular
disease may be difficult to diagnose. (42 FR 28602 at 28608.)
While AHP argues that difficulties in making a diagnosis are what
prevented the Rao study from distinguishing Alzheimer's patients from
others, the fact remains that the Rao study was neither looking for nor
attempting to identify Alzheimer's patients as that disease is
currently defined, i.e., including patients with an onset of dementia
over the age of 50. Rather, the Rao study primarily used an age cut off
to identify Alzheimer's patients under the old definition. To
retrospectively identify Alzheimer's patients under the current
definition for Alzheimer's disease would require adequate information
in the patient records which could be used to support the diagnoses.
This information is not available in the Rao study records.
As was stated in the Commissioner's Decision on Lutrexin, ``(T)he
law is clear that the applicant must provide substantial evidence of a
drug's effectiveness under its labeled conditions of use, not those
under which an investigator chooses to test it.'' (41 FR 14406 at
14419). Therefore, for all of the aforementioned reasons, I find that
the Rao study was not adequate and well-controlled in that it failed to
show that Cyclospasmol was tested in Alzheimer's patients.
c. Concomitant diseases and conditions. AHP further argues that the
ALJ erred in ruling that the Rao study was not adequate and well-
controlled because the ALJ found that patients with strokes, histories
of alcoholism, severe diabetes, and Parkinson's disease were admitted
to the study, although these patients were to have been excluded under
the protocol. (AHP Exceptions 125-26, citing I.D. at 42, 56.) In all,
the Center identified 18 patients with concomitant diseases or
conditions, including 3 patients with multiple conditions, whom they
claim should have been excluded. (Center Exceptions at 5-6; Center
Post-Hearing Brief at 53-62, & Attachment A.)
AHP concedes that protocol violations occurred, but argues that
inclusion of most of these patients resulted in mere technical
violations of the protocol and did not confound the results of the
study. (AHP Exceptions at 126-28.) AHP further states that the Rao
protocol was overly rigid, and that it was a question of medical
judgment and expertise as to whether these protocol violations affected
the study results. (AHP Post-Hearing Brief at 90, 93.)
The stated objective of the Rao study was ``to evaluate the
efficacy of Cyclospasmol'' in alleviating symptoms of
senescence commonly
[[Page 64118]]
associated with cerebral vascular insufficiency.'' (G-28.8 at 314.)
Towards this end, the protocol provided for the exclusion of patients
with dementia caused by other conditions. In relevant part, the
protocol's exclusionary criteria read as follows:
Patients exhibiting any one of the following will be excluded
from the study:
1. Those with a history of CVA (cerebral vascular accident,
i.e., stroke (See A-121 at 28)).
2. Those who, upon physical examination, demonstrate
neurological evidence of a past CVA.
* * * * *
8. Those with severe diabetes mellitus which requires insuli(n)
therapy, or with evidence of glycosuria on urinalysis or who exhibit
complication of diabetes.
* * * * *
10. Those with any other severe disease: e.g. significant
hematologic disorders; history of malignant disease within one (1)
year; recent (4 months) major surgical procedure; pulmonary embolism
within one (1) year; severe chronic infection; severe renal, hepatic
or neurological disorder, except the one being studied herein * * *.
* * * * *
12. Those whose symptoms of senescence occurred prior to age
fifty (50).
13. Those with a history of alcohol or other drug abuse, except
that patients with a history of alcoholism prior to age 45, with no
recurrence after that age, may be entered if the investigator feels
that the patient's alcoholism did not contribute to his present
symptoms.
14. Those with a history of major psychiatric illness.
(G-28.8 at 315-16.)
Relying upon the protocol, the Center identifies numerous patients
whom it contends were admitted in violation of the exclusion
provisions. I will address each type of alleged violation in turn.
i. Strokes. The Center first specifies seven patients, identified
as Numbers 3, 12, 15, 21, 31, 45 and 64, as having histories of strokes
and therefore subject to exclusion. (Mohs, G-62 at 8-9; Thal, G-63 at
6; Leber, G-64 at 10-15; Leber, G-64, Attachment B at 2; Denton, A-121
at 25, 27-28, 74, 76, 77, 79, 83, 85; Denton Tr. Vol. VII at 16-17; G-
14.6 at 351.)
AHP concedes that Patient Nos. 12 and 64 should be excluded (AHP
Post-Hearing Brief at 91; Denton, A-121 at 28), but argues against
excluding the other five patients, on the grounds that the protocol was
overly rigid because it excluded patients whose strokes occurred 2 to 3
years prior to the start of the Rao study. (AHP Post-Hearing Brief at
93.)
In support of its position that these stroke patients need not be
excluded, AHP cites to the testimony of Dr. Clarence Denton, a witness
for AHP, who testified as follows:
Generally, there is no need to exclude patients on the basis of
a stroke which occurred more than two to three years prior to the
onset of the study. Strokes which occurred shortly before the onset
of the study should be excluded, however, because the natural
recovery process which occurs soon after a stroke is suffered could
make it appear that a drug (or placebo) was having a favorable
action. Ordinarily, normal recovery from a stroke would occur within
six months to one year of the occurrence of the stroke. From a
practical standpoint, therefore, it is perfectly reasonable to
include patients whose strokes occurred many years prior to the
onset of the study, as long as dementia is still present.
(Denton, A-121 at 26.)
It is beyond cavil that patients having a history of strokes were
to be excluded under the protocol. Inclusion of these patients was a
clear protocol violation. The question now is what effect do these
protocol violations have on the validity of the study.
I begin my review of these protocol violations by noting that some
protocol violations may be inadvertent or unavoidable on the part of
those conducting the study, such as occurs with the failure of a study
subject to follow the study's drug regimen. However, other protocol
violations may reflect a lack of attention to the requirements of the
protocol by those conducting the study. (Commissioner's Decision on
Benylin, 44 FR 51512 at 51531 (The inclusion of subjects who did not
meet the entrance criteria of the study ``suggests inattention to
detail'' and can ``be considered in deciding whether the study was
adequate and well-controlled.'').) Failure to follow inclusion/
exclusion criteria, such as occurred in the Rao study, can be an
indication of such inattention to the details of a study's protocol.
Even violations which by themselves may not warrant rejection of a
study can be considered in the aggregate in determining whether a study
is adequate and well-controlled. (Commissioner's Decision on Benylin,
44 FR 51512 at 51531.) Evidence of any protocol violation, even if
inadvertent or unavoidable, is relevant to the issue of whether the
study is adequate and well-controlled. Therefore, I rule that inclusion
of the seven stroke patients, both the two patients whom AHP concedes
should be excluded and the five whom AHP disputes, properly can be
considered as protocol violations and weighed in the review of the Rao
study.
ii. Alcoholism. The Center further argues that five subjects--
Patient Nos. 16, 22, 32, 54, and 63--should have been excluded because
they were suffering from alcoholism. (Mohs, G-62 at 9; Thal G-63 at 6;
Leber, G-64 at 10-12; Denton, A-121 at 28-29, 42, 77, 79, 84, 85;
Denton, Tr. Vol. VII at 22-24; A-126 at 17-20, 22-25.)
AHP makes an argument only against the exclusion of Patient No. 16.
(AHP Post-Hearing Brief at 93; AHP Exceptions at 129.) AHP cites to the
testimony of Dr. Denton, who testified that Patient No. 16 had consumed
no alcohol for 3\1/2\ years before the start of the study, and that the
initial psychiatric consultation diagnosed both cerebral
arteriosclerosis and chronic alcoholism. (Denton, A-121 at 28-29.)
Because of the diagnosis of cerebral arteriosclerosis, Dr. Denton
suggested that it is unlikely that alcoholism is the primary cause of
the dementia in Patient No. 16. (Id. at 29.)
Although in the practice of medicine it is expected that a
physician may be called upon to treat patients with concomitant
illnesses, in clinical drug trials it is necessary to exclude patients
with any concomitant conditions that may confound the results of the
study. Aside from the fact that Dr. Denton offers no facts to support
his position regarding Patient No. 16, I conclude that, at the very
least, alcoholism was a confounding factor with this patient. It is
clear that Patient No. 16 should have been excluded, as should the
other four patients (Nos. 22, 32, 54, and 63) who also had alcoholism.
iii. Severe diabetes. The Center next argues that three subjects--
Patient Nos. 23, 29, and 32--had severe diabetes, a basis for exclusion
under the protocol. (Mohs, G-62 at 9; Thal, G-63 at 6; Leber, G-64 at
13; Denton, A-121 at 32, 80; A-126 at 21.)
AHP takes issue with only the exclusion of Patient No. 32. (AHP
Post-Hearing Brief at 92; AHP Exceptions at 130.) AHP argues that it
was not necessary to exclude Patient No. 32 because this patient's
diabetes was not severe enough to be insulin dependent. (AHP Exceptions
at 130; Denton, A-121 at 32.) I find AHP's arguments with regard to
this patient to be moot, since AHP has already conceded that Patient
No. 32 should be excluded for alcoholism. (See section I.D.1.c.(2). of
this document.)
iv. Severe diseases, Parkinson's disease, psychiatric illness, and
other diseases. The Center argues that three other patients--Nos. 20,
31 and 59--had severe, chronic infections, which was a basis for
exclusion under the protocol. (Center Post-Hearing Brief at 56-57; see
G-28.8 at 315-16.) The Center first argues that Patient No. 20 should
have been excluded because this patient had active pulmonary
tuberculosis. (Center
[[Page 64119]]
Exceptions at 7-8, citing Mohs, G-62 at 9; Leber, G-64 at 11-12.)
Regarding Patient No. 20, Dr. Leber, a Center witness, testified that
``(a)dequate treatment of his condition rather than treatment with
Cyclospasmol may easily have accounted for the patient's 3.0
improvement on Item 19 of the SCAG.'' (Leber, G-64 at 15.)
AHP argues that the diagnosis of severe pulmonary tuberculosis was
incorrect for Patient No. 20, and cites to the testimony of Dr. Denton,
an AHP witness, who undertook a post-study review of records for the
Rao study. (AHP Reply to Center Exceptions at B-6, citing Denton, Tr.
Vol. VII at 28-33; AHP Post-Hearing Brief at 91.) In his testimony, Dr.
Denton agreed that the patient records showed that Patient No. 20 was
treated with anti-tuberculous drugs (see G-14.6 at 77), and further
agreed that the records reflect that this patient was diagnosed during
the study as having pulmonary tuberculosis with chronic brain syndrome
(see G-14.6 at 53, 55), but nevertheless disputes the diagnosis. Dr.
Denton based his challenge to the diagnosis on the absence in the
patient records of the actual X-ray report and the absence of the
sputum examination. (Denton, Tr. Vol. VII at 30.)
I am not persuaded by Dr. Denton's testimony on this point. I find
that there is sufficient evidence in Patient No. 20's records to
support a conclusion that this patient did have severe pulmonary
tuberculosis. There are several notations in this patients' records
which state that this patient had pulmonary tuberculosis. (See, e.g.,
G-14.6 at 53, 55.) Under the protocol, this patient appropriately
should have been excluded.
The Center also argues that Patient Nos. 31 and 59 should have been
excluded because these patients had severe, chronic infections. (Center
Post-Hearing Brief at Attachment A, citing Thal, G-63 at 6.) However,
the Center does not identify the types of chronic infections which
these two patients were said to have had. I reviewed the extant patient
records, but these records were not always legible and I was unable to
determine what type of infections these patients had. Therefore, in
absence of more specific evidence, I rule that Patient Nos. 31 and 59
should not be excluded.
The Center further argues that two subjects, Patient Nos. 56 and
63, had Parkinson's disease. (Thal, G-63 at 6-7; Leber, G-64 at 14.)
AHP concedes that both of these patients should be excluded, and I
accept AHP's concession on this matter. (AHP Exceptions at 130; Denton,
A-121 at 29, 35, 84-85.)
The Center also argues that Patient No. 9 should have been excluded
because this patient had a major psychiatric illness, i.e., hysterical
personality. (Leber, G-64 at Attachment B, p.2.) AHP similarly concedes
that this patient should have been excluded, and I also accept this
concession. (Denton, A-121 at 33, 75.)
The Center next argues that Patient No. 32 had grand mal epilepsy
and should have been excluded for this reason. (G-14.7 at 9; A-126 at
21; Denton, Tr. Vol. VII at 20-21.) I need not reach the merits of this
argument because AHP has already conceded that Patient No. 32 should be
excluded for alcoholism. (See section I.D.1.c.(2). of this document.)
d. Concomitant Medications. AHP further argues that the ALJ erred
in ruling that the widespread administration of concomitant medications
precluded any meaningful analysis of the effects of
Cyclospasmol in the Rao study. (AHP Exceptions at 132, citing
I.D. at 37, 42, 56.) In support of its argument, AHP cites to a
previous Commissioner's Decision pertaining to the human drug, Oral
Proteolytic Enzymes (OPE), in which it was ruled that a study may be
used to demonstrate efficacy ``if the identity, quantity, strength,
frequency, and length of administration of the concomitant medication
is known and if the confounding effect of the concomitant medication
has been analyzed so that the effect of the test drug can be
determined.'' (Commissioner's Decision on OPE, slip op. at 52-53
(footnote omitted).) AHP argues that under the OPE decision, the ALJ
failed to analyze sufficiently whether the concomitant medications had
any effect on the study results.
In the Commissioner's OPE decision, it was noted that ``(t)he
uncontrolled use of concomitant medication violates several of the most
basic scientific principles governing clinical investigations.''
(Commissioner's Decision on OPE, slip op. at 47.) Three such scientific
principles, all of which have been incorporated into FDA regulations,
were cited by the Commissioner's Decision on OPE.
The first of these principles, as articulated in the regulations,
requires that ``(t)he method of assigning patients to treatment and
control groups minimizes bias and is intended to assure comparability
of the groups with respect to pertinent variables such as * * * use of
drugs or therapy other than the test drug.'' (Sec. 314.126(b)(4) (At
the time of the Commissioner's Decision on OPE, the citation for the
comparable regulation was 21 CFR 314.111(a)(5)(ii)(a)(2)(iii)).) The
objective of this requirement is to limit, before the study has begun,
the extraneous factors which could be responsible for a difference
between groups. (Commissioner's Decision on OPE, slip op. at 47-48.) If
the assignment of patients is biased, this can skew the study's
results.
The second relevant principle, also incorporated into agency
regulations, is a requirement that ``(t)he study uses a design that
permits a valid comparison with a control to provide a quantitative
assessment of drug effect.'' (Sec. 314.126(b)(2) (The comparable
numbered section of the regulations at the time of the Commissioner's
Decision on OPE was Sec. 314.111(a)(5)(ii)(a)(4)).) The use of
concomitant medication can make it impossible to state with accuracy
whether the results of a study were due to the test drug under study or
were due to the use of concomitant medication. (Commissioner's Decision
on OPE, slip op. at 48-50.)
Thirdly, the Commissioner's Decision on OPE ruled that concomitant
medication use must be sufficiently documented so that a scientific
evaluation of the use of concomitant medication can be done.
(Commissioner's Decision on OPE, slip op. at 50-53.) If a study lacks
sufficient documentation of concomitant medication use, the study
cannot be considered as part of the basis for approval of effectiveness
claims. (Id.) This requirement is expressed in the regulatory
requirement that the report of a study ``provide sufficient details of
study design, conduct, and analysis to allow critical evaluation and a
determination of whether the characteristics of an adequate and well-
controlled study are present.'' (Sec. 314.126(a) (The comparable
numbered section of the regulations at the time of the Commissioner's
Decision on OPE was 21 CFR 314.200(d)(2)).)
Regarding the review of concomitant medication, I note that the
Commissioner's Decision on OPE further states that the use of
concomitant medication must be considered as ``a fatal flaw'' in the
absence of detailed records which would permit evaluation of the effect
of the concomitant medication on the results of the study.
(Commissioner's Decision on OPE, slip op. at 52.) The burden is on the
proponent of the drug to supply detailed records demonstrating the
effects of the concomitant medication on the results of the study.
(Commissioner's Decision on OPE, slip op. at 134, 144, 203-04.)
[[Page 64120]]
As for the Rao study, I have reviewed the ALJ's decision, and I
find that the ALJ considered each instance of concomitant medication
use. (See I.D. at A-1 to A-5.) Contrary to AHP's claim, the ALJ did not
base his decision solely upon the number of patients who were given
concomitant medication. As was observed in the Commissioner's OPE
decision, ``the use of more than one concomitant medication increases
the difficulty of the evaluation of the (study drug's) effect.''
(Commissioner's Decision on OPE, slip op. at 56 (footnote omitted).)
While the number of patients given concomitant medication was one
factor which properly was considered by the ALJ (Commissioner's
Decision on OPE, slip op. at 57), a review of the ALJ's complete
decision reveals that the ALJ also considered the identity, quantity,
strength, frequency, and length of administration of the various
concomitant medications. (See I.D. at A-1 to A-5.) The ALJ took the
cited portion of the Commissioner's Decision on OPE into consideration
when the ALJ ruled that the concomitant medications ``were so numerous
and so pervasive in the Rao study as to preclude any meaningful
analysis of the test drug.'' (I.D. at 37.)
AHP also made arguments regarding the individual patients'
concomitant drug use. (AHP Post-Hearing Brief at 96-99.) The Center,
based upon a review of the hospital records, identified 16 different
concomitant medications used by 21 patients in the Rao study,5
including Patient No. 1 (Valium, Compazine), Patient No. 2 (Mellaril),
Patient No. 6 (Valium), Patient No. 9 (Haldol, Benadryl), Patient No.
10 (Valium), Patient No. 14 (Valium), Patient No. 17 (Valium,
Mellaril), Patient No. 22 (Mellaril), Patient No. 23 (Seconal), Patient
No. 24 (Aldomet), Patient No. 28 (Hydergine), Patient No. 29 (Mellaril,
Insulin, Doxepin), Patient No. 32 (Phenobarbital, Dilantin), Patient
No. 36 (Haldol, Seconal, Meprobamate), Patient No. 42 (Seconal),
Patient No. 43 (Seconal, Peritrate), Patient No. 45 (Mellaril,
Peritrate), Patient No. 51 (Mellaril), Patient No. 56 (Valium,
Sinemet), Patient No. 57 (Compazine), and Patient No. 68 (Thorazine).
The Center argued that the confounding effect of the concomitant
medications used by these patients made the Rao study results
unreliable. (Center Post-Hearing Brief at 65.)
---------------------------------------------------------------------------
5 The Center also argues that Patient No. 2 in the Rao
study should be excluded because this patient had been given Elavil,
which was a violation of the protocol. The Center further argues
that Patient No. 24 had received Serax, and Patient No. 34 had
received Phenergan in violation of the protocol. However, my review
of the records reveals that it was Patient Nos. 2, 24, and 34 in the
Yesavage study, not the Rao study, who had taken these drugs.
Accordingly, these issues will be addressed in the discussion of the
Yesavage study.
---------------------------------------------------------------------------
I note, however, that of these 21 patients, AHP has already
conceded that 9 patients (Patient Nos. 9, 22, 23, 29, 32, 36, 43, 56,
68) should be excluded for violations of the inclusion/exclusion
criteria. (See section I.D.1.c. of this document.) Additionally, Dr.
Denton, a witness for AHP, conceded that Patient No. 36 should be
excluded because this patient was taking the concomitant medication,
Seconal, a psychoactive drug, and Haldol, a major tranquilizer, at the
time of final evaluation. (Denton, A-121 at 81-82.) Remaining after
these nine conceded exclusions are 12 patients who received 7 different
drugs, including Patient No. 1 (Valium, Compazine), Patient No. 2
(Mellaril), Patient No. 6 (Valium), Patient No. 10 (Valium), Patient
No. 14 (Valium), Patient No. 17 (Valium, Mellaril), Patient No. 24
(Aldomet), Patient No. 28 (Hydergine), Patient No. 42 (Seconal),
Patient No. 45 (Mellaril, Peritrate), Patient No. 51 (Mellaril), and
Patient No. 57 (Compazine). I will address the issues concerning these
remaining, contested exclusions.
However, before I address the specific records for each patient, I
will make some general observations regarding all the patient records
in evidence from the Rao study. First, it must be noted that the
contents and status of the patient records in evidence is not
consistent from patient to patient. Most records appear to contain only
excerpts from the original records. Some records include numerous pages
from the physician order sheets, medication records, nursing care
record sheets, and patient progress notes. (See, e.g., Patient No. 24,
G-14.6 at 175-209.) Other patient records contain only a single page.
(See, e.g., Patient No. 18, G-14.6 at 30.) Then again, other records
contain a few pages of various sections from the original patient
records. (See, e.g., Patient No. 2, G-14.5 at 51-62.)
In addition to the difficulty presented by the inconsistent content
of the patient records, another problem is legibility of records. In
some instances, although records are in evidence, portions of those
records are printed so faintly as to be illegible. (See, e.g, Patient
No. 1, G-14.5 at 32, 34, 39, 41; Patient No. 42, G-14. 7 at 245-264;
Patient No. 45, G-14.7 at 320.)
Another problem I have found with the records in evidence is the
difficulty in identifying the dates on which the patient was evaluated
during the study. The protocol provided that ``(e)ach patient will be
observed four (4) times. These observations will be made at the initial
evaluation and at weeks 4, 8, 12.'' (G- 14.2 at 241.) The dates of
these evaluations are important to a review of concomitant medication
use because the protocol also provided that ``no major tranquilizer
should be administered within the four (4) days immediately proceeding
(sic) any evaluation.'' (G-14.2 at 243.)
In reviewing the patient records, I noted that, despite the
requirements of the protocol, in a number of patient records the dates
on which the patient received the study drug and the dates of the
patient evaluations are not consistent with the specifications of the
protocol. For example, in the physician order sheets and in the
medication records for Patient No. 1, evidence indicates that this
patient began to receive the study drug on December 17, 1975, and
continued to receive this drug until March 19, 1976. (G-14.5 at 13-16,
21, 23, 25, 27.) However, other documents in evidence indicate that
this patient was initially evaluated on January 14, 1976, 1 month after
the patient began to receive the study drug. (G-14.5 at 10.) Additional
documents in evidence also point to a delayed evaluation occurring in
January. For example, one document lists a date of February 25, 1976,
and states, ``Mental Status: Second evaluation during the fourth
week.'' (G-14.5 at 9.) Another document lists the date of May 11, 1976,
as the date of the third evaluation. (G-14.5 at 8.)
It is difficult to fathom why the initial evaluation would have
occurred a month after the study had begun, but the dates in the
records of a number of other patients clearly support this conclusion.
(See also Patient No. 6, G-14.5 at 153, 154; Patient No. 17, G-14.6 at
14, 18.) I further noted that this 1 month difference in dates is not
found consistently in all patient records. (See, e.g., Patient No. 57,
G-14.8 at 132, 135 (initial evaluation and start of study drug occurred
on same date.)) Of course, an initial evaluation that occurred 1 month
after the start of the study drug would be a protocol violation and
would not be the proper procedures for an adequate and well-controlled
study. An initial evaluation of the patient should be taken before the
patient has been randomized in the study.
I also noted that while most patient records in evidence contained
a page from a psychological evaluation which was captioned at the top
``Final Evaluation,'' I found that the date of this evaluation in many
instances appeared to be from the middle of the study, often closer to
week 8 than to the actual time of final evaluation at week 12. (See,
e.g.,
[[Page 64121]]
Patient No. 25, G-14.6 at 210-213; Patient No. 26, G-14.6 at 234-237.)
However, not all patient records follow this pattern. In some cases,
the date on the ``Final Evaluation'' document does appear to have
occurred 12 weeks after the patient started on the study drug. (See,
e.g., Patient No. 45, G-14.7 at 310, 312.) Therefore, I did not find
the date on the document entitled ``Final Evaluation'' to be a reliable
means of establishing the dates of the patients' final evaluations in
many instances.
Also, I have found several records in which the physician order
sheets or medication records indicate that the patient had been
receiving the test drug for a month before the recorded date of the
patient's initial evaluation. (See, e.g., Patient No. 1, G-14.5 at 10,
13; Patient No. 3, G-14.5 at 68, 73; Patient No. 26, G-14.6 at 235,
239.)
Nevertheless, despite these flaws I have given the patient records
full consideration. These records were closely scrutinized for
pertinent dates and schedules of relevant medication use. However, AHP,
as sponsor of these studies, bears the responsibility of providing
adequate records for review. For this reason, any failure of the
records to document concomitant medication use can be weighed against
finding the Rao study adequate. (Commissioner's Decision on OPE, slip
op. at 50-53.) With this as background, I turn now to the specifics of
each use of concomitant medication now at issue.
The Rao protocol's requirements regarding concomitant medications
were as follows:
No vasodilating agents, psychoactive drugs, narcotics, reserpine
derivatives or steroids other than estrogen will be permitted during
the study, except for an h.s. (hora somni, i.e., at bedtime)
hypnotic, which may be either Noludar or chloral hydrate, or an
occasional dose of a major tranquilizer (phenothiazines,
haloperidol, etc.) deemed necessary for the patient's welfare.
However, any patient who receives more than sixteen (16) doses of a
major tranquilizer during the entire course of the study, or more
than three (3) doses in any one week, will be dropped from the
study. Also, no major tranquilizer should be administered during the
four (4) days immediately proceeding (sic) any evaluation. Other
routine drugs (e.g. digitalis, diuretics, oral hypoglycemics, non-
narcotic analgesics, antibiotics, etc.) required by the patient may
be administered, but every effort should be made to maintain a
consistent dosage schedule. Patients who have been receiving agents
not permitted during the study should have them discontinued 21 days
prior to entry.
(G-28.8 at 318.)
Regarding the use of concomitant medication, the Center first
argues that Patient No. 1 should be excluded because this patient
received both Valium and Compazine during the course of the study.
(Center Post-Hearing Brief at 64 and Attachment B; G-14.5 at 20-28;
Thal, G-63 at 7.) Valium, a benzodiazepine, is a psychoactive drug,
given to reduce anxiety; this drug can cause drowsiness, and affect
attention and alertness. (Leber, G-64 at 14; Zung, Tr. Vol. III at 38;
Denton, Tr. Vol. VII at 25-26.) Compazine, also a psychoactive drug,
may impair mental and physical abilities. (Denton, Tr. Vol. VII at 39.)
The frequency of administration of Valium given to Patient No. 1 is
particularly troubling. According to the testimony of Dr. Denton, this
patient was given 23 doses of Valium during the study. (Denton, A-121
at 72; see also G-14.5 at 20-28; I.D. at A-1.) Specifically, this
patient received Valium 11 times between December 18 to December 23,
1975, 5 times between January 24 to January 31, 1976, 8 times between
February 14 to February 22, 1976, and 4 times between March 2 to March
5, 1976. (Denton, A-121 at 72; I.D. at A-2; G-14.5 at 13-49.) In
addition, at least 5 doses of Valium were given during the prestudy
washout period. (I.D. at A-2; G-14.5 at 13-28.) Moreover, the time of
administration of the Valium is not always clearly indicated in the
record. This is a clear violation of the protocol, which provided that
no psychoactive drugs, except for a bedtime dose of Noludar or chloral
hydrate, were permitted. (G-28.8 at 318.) Accordingly, I am in
agreement with the ALJ in finding that this is no mere technical
violation of the protocol, and that Patient No. 1 should be excluded.
The Center also argues that Patient No. 6 should be excluded for
receiving Valium during the study. (Center Post-Hearing Brief at 64 &
Attachment B.) The ALJ ruled that this patient should have been
excluded because medication records appeared to indicate that this
patient had received Valium throughout the course of the study. (I.D.
at A-1.) The ALJ cited to the fact that the copy of the medication
records in evidence shows a line drawn across all dates in the chart
entry for Valium. (I.D. at A-1, citing G-14.5 at 154.) AHP challenges
the ALJ's interpretation of the medication records, arguing that the
referenced markings on Patient No. 6's chart do not support a finding
that the patient was given Valium on those days. (AHP Post-Hearing
Brief at 97.)
I have reviewed the cited portion of the medication records for
Patient No. 6, and I find that the medication chart in question does
show an arrow drawn across all dates in the chart. (G-14.5 at 154.)
There are also notations in the margins next to this Valium entry which
read, ``Start 12/31,'' ``Valium 10 mg. `IM' daily,'' ``q 8 deg.,'' and
``Stop 3/19,'' or it may be ``Stop 5/19,'' the writing is not clear.
(G-14.5 at 154.) However, my interpretation of this entry is that this
particular chart was begun on December 31, and the arrow across the
chart was intended to delete the earlier days in the month of December,
and was not meant to reflect dosages on those earlier dates. Therefore,
I find that the ALJ was in error in his interpretation of this
particular chart.
Notwithstanding my ruling with regard to the previously mentioned
chart, I find that other records in evidence do support a finding that
Patient No. 6 was receiving regular doses of Valium at later dates
throughout the study. Aside from the aforementioned chart entries,
there are several other chart entries which state that 10 mg of Valium
was to be given intramuscularly every 8 hours, commencing on December
31, 1975, and running through March 9, 1976. (G-14.5 at 154, 155, 156,
157.) During this same time, Patient No. 6 was receiving the study
drug. (G-14.5 at 154, 155, 156, 157.) The extent of Valium
administration was a clear violation of the protocol's general
prohibition on the use of psychoactive drugs except for bedtime doses
of Noludar or chloral hydrate. (G-28.8 at 318.) Therefore, I affirm the
ALJ's ruling in excluding Patient No. 6.
As for Patient No. 17, the physician order sheet states that
Patient No. 17 was to receive chloral hydrate PRN (pro re nata, as
occasion arises) during the study (G-14.6 at 19, 21), and evidence
indicates that the patient received this drug on several occasions.
(Mohs, G-62 at 9-10.) I note, however, that chloral hydrate at bedtime
was permitted under the protocol, and I do not find this to be a basis
for excluding this patient. (G-28.8 at 318.)
The Center also argues that Patient No. 17 received both Valium and
Mellaril on several occasions, and that this is a basis for excluding
this patient. (Center Post-Hearing Brief at Attachment B; Mohs, G-62 at
9-10.) As previously discussed, Valium is a psychoactive drug. The use
of psychoactive drugs was generally prohibited except for bedtime doses
of Noludar or chloral hydrate. (G-28.8 at 318.) Mellaril, on the other
hand, would fall under the category of a major tranquilizer under the
protocol, of which occasional doses were permitted if necessary for the
patient's welfare. (G-28.8 at 318.)
I have reviewed the extant charts for Patient No. 17, and I have
found that the
[[Page 64122]]
physician order sheets contain a notation, dated December 18, 1975, to
run through February 18, 1976, which reads, ``Valium 10 mg I.M.
(intramuscularly) PRN.'' (G-14.6 at 17.) Another entry in the physician
order sheets, dated February 18, 1976, directed that the Valium order
be continued through April 19, 1976. (G-14.6 at 20.) Entries on the
nursing care records, which are illegible in sections, indicate that
Patient No. 17 received 10 mg of Valium intramuscularly on at least
five occasions. (G-14.6 at 23-25.) The record indicates administration
of Valium on December 16 and 21, 1975, and on January 1, January 9, and
January 14, 1976. It also appears from the record that this patient
began receiving the study drug on December 19, 1975. (G-14.6 at 18.)
The physician order sheets further show that on December 18, 1975,
orders were given for Patient No. 17 to receive 25 mg of Mellaril, an
antipsychotic drug, ``t.i.d.'' (ter in die, three times a day),
beginning during the final 2 days of the washout period. (G-14.6 at 17;
see also Leber, G-64 at 11; Mohs, G-62 at 9-10.) However, another chart
entry, dated December 19, 1975, ordered the Mellaril discontinued. (G-
14.6 at 18.) The nursing care records do not record the administration
of Mellaril.
With regard to the dates of evaluation of Patient No. 17, I note
that there are significant inconsistencies in this patient's records.
While the physician's order sheets indicate that Patient No. 17 was
started on the study drug on December 19, 1975 (G-14.6 at 18), another
document in the record indicates that this patient's initial evaluation
occurred on January 19, 1976 (G-14.6 at 14), 1 month after the patient
had been on the study drug. This January date for the initial
evaluation is consistent with another record entry, which lists the
date for the ``(s)econd evaluation during the fourth week'' as being on
February 25, 1976. (G-14.6 at 13.) But in apparent contradiction to the
January date, yet another record item, this one found in the patient
progress notes, dated January 23, 1976, states that the patient ``is on
vasodilator drug Cyclospasmol for another month.'' (G-14.6 at
15.) This would place this patient's initial evaluation at sometime in
November 1975, and final evaluation in February 1976.
These inconsistencies, along with the illegibilities and obvious
incompleteness of the record (there are large gaps of at least two
months duration between dates in the patient progress records), make
the records of Patient No. 17 inadequate for proper review. Therefore,
I find that this patient should be excluded. (Commissioner's Decision
on OPE, slip op. at 50-53.)
Regarding Patient No. 24, Dr. Paul Leber, a witness for the Center,
testified that there were several interruptions in treatment with
Cyclospasmol between the dates of February 18, and February
22, 1976, during the study. (Leber, G-64 at 12.) I have reviewed the
physician's order sheet for this patient, and I have found that the
records do show that Cyclospasmol was discontinued on
February 18, but was started again on February 22, 1976. (G-14.6 at
182, 183.) I note Patient No. 24's records indicate that this patient's
initial evaluation was on January 26, 1976, and the patient's final
evaluation was on May 7, 1976. (G-14.6 at 175, 177.) In view of the
brevity of the interruption, and the fact that it did not occur close
to the time of either the initial or the final evaluation, I do not
find this a basis to exclude Patient No. 24.
Dr. Leber also testified that Patient No. 24 received Aldomet, an
antihypertensive medication which can affect mood and cognition.
(Leber, G-64 at 13.) Dr. Leber testified that ``the protocol (was)
unclear as to whether such patients could or could not have been
admitted, but discontinuation of this medication (Aldomet) might affect
a patient's mental status.'' (Leber, G-64 at 13.)
In considering the administration of Aldomet to Patient No. 24, I
note that the protocol provided that ``routine drugs (e.g., digitalis,
diuretics, oral hypoglycemics, non-narcotic analgesics, antibiotics,
etc.) required by the patient may be administered, but every effort
should be made to maintain a consistent dosage schedule.'' (G-14.2 at
243.) I would place Aldomet in the category of routine drugs for the
purposes of the Rao study. As for the schedule of administration of
Aldomet to Patient No. 24, the physician's order sheets indicate that
this patient was receiving 250 mg of Aldomet four times a day from
November 14, 1975 (G-14.6 at 186), until February 16, 1976. (G-14.6 at
184.) As I previously noted, this patient's initial evaluation was on
January 26, 1976, and the final evaluation was on May 7, 1976. (G-14.6
at 175, 177.) Thus, this patient was receiving Aldomet throughout the
washout period and continuing through several weeks of the study.
Having considered Patient No. 24's use of Aldomet, I find that this
is not a basis to exclude this patient. At the time of initial
evaluation, this patient was well-established on the regimen of
Aldomet, which could mean that any initial drowsiness which the patient
might have experienced may have passed. As for the withdrawal of
Aldomet during the study, I do not find the evidence of any negative
effects on the patient to be sufficient to exclude this patient.
Therefore, I uphold the ALJ's decision to include Patient No. 24 in the
Rao study. (I.D. at A-2.)
The Center next argues that Patient No. 28 should be excluded for
receiving Hydergine during the study. (Center Post- Hearing Brief at 64
& Attachment B.) Evidence indicates that this patient received
Hydergine three times a day during the first week of the study.
(Denton, A-121 at 80; Thal, G-63 at 7; G-14.6 at 261-62.) Regarding the
effect of this drug, Dr. Denton testified, ``Hydergine is an agent
which helps to relieve some of the cognitive aspects of dementia
through an unknown mechanism of action.'' (Denton, A-121 at 39; see
also Zung, Tr. Vol. III at 64.) However, Dr. Denton suggested that
Patient No. 28 did not have to be excluded because Hydergine was
administered during the first week of the study in December 1975, and
this should not have affected the final evaluation made in March 1976.
(Denton, A-121 at 40.)
I have reviewed the records in evidence for Patient No. 28, and I
found that the physician order sheets indicate that this patient was
receiving Hydergine for at least two months prior to the start of the
Rao study. (G-14.6 at 261, 262, 265.) To the extent that Hydergine is
effective, then Patient No. 28's baseline might have been higher than
it would have been otherwise. The withdrawal of Hydergine could have
caused a worsening in the patient's condition over the course of the
12- week study. I therefore find that the possible confounding effect
of Hydergine must be considered, and that for this reason, Patient No.
28 should be excluded.
Regarding Patient No. 42, Dr. Denton testified that this patient
received Seconal at bedtime during the final week of the study, from
March 27 to April 2, 1976. (Denton, A-121 at 82.) As Dr. Denton
acknowledged, Seconal is a psychoactive medication, and, as such, its
use was generally prohibited under the protocol. (Denton, A-121 at 81
(discussing Patient No. 36); G-28.8 at 318.) Nevertheless, Dr. Denton
takes the position that this is not a reason to exclude Patient No. 42,
notwithstanding the fact that the medication was given at the time of
final evaluation. (Denton, A-121 at 82.)
First, I note that this patient's use of Seconal does not appear to
be documented in the patient records in evidence; however, I also note
that
[[Page 64123]]
many of this patient's records are not legible. (G-14.7 at 219-264.)
The question of documentation was not raised by the Center; rather, the
Center's arguments are based on the violation of the concomitant
medication restrictions in the protocol.
Because the averred level of use of Seconal was that of a bedtime
hypnotic, I find that, while Patient No. 42's concomitant medication
use violated the protocol's general prohibition on psychoactive drugs
except for bedtime doses of Noludar or chloral hydrate (G-28.8 at 318),
this level of use is not cause for excluding Patient No. 42.
Nevertheless, I note that AHP's failure to provide documentation for
the administration of Seconal can be considered as a flaw in the Rao
study and can be weighed in evaluating the adequacy of this study.
(Commissioner's Decision on OPE, slip op. at slip op. at 52-53.)
Additionally, the fact of this protocol violation can also be
considered in evaluating this study.
Regarding Patient No. 45, evidence indicated that this patient
received 20 mg of Peritrate, a vasodilator, twice a day during the
study, from March 23 to March 31, 1976. (G-14.7 at 314; Denton, A-121
at 39, 82-83; Mohs, G-62 at 11.) Patient No. 45's records do not
indicate the date of initial evaluation, but, from an entry on the
physician's order sheet, it appears that this patient had been
receiving the study drug since January 5, 1976. (G-14.7 at 312.)
Another entry in this patient's progress notes states that, as of March
7, 1976, this patient had been on Cyclospasmol for 2 months,
which would be consistent with an initial date of January 5, 1976. (G-
14.7 at 318.) Final evaluation of this patient apparently was on April
8, 1976. (G-14.7 at 310.) Evidence also indicates that Patient No. 45
was receiving an unspecified level of Mellaril during the washout
period. (Denton, A-121 at 83.) The Center argues that because of these
concomitant medications, Patient No. 45 should be excluded. (Center's
Post-Hearing Brief at 64.)
In Dr. Denton's written review of Patient No. 45, Dr. Denton wrote
that Mellaril was given prior to the study, but was discontinued on
December 26, 1975, about 10 days before the study drug was started.
(Denton, A-121 at 83.) Regarding the Peritrate, Dr. Denton concluded
that the use of this drug for a period of one week was ``irrelevant.''
(Denton, A-121 at 83.)
I have reviewed the records in evidence for Patient No. 45, but
these records, which are illegible in parts, do not appear to contain
the chart of administration of Mellaril. (See G-14.7 at 310-333.) While
the absence of complete records can be considered a ``fatal flaw'' for
the adequacy of a study (Commissioner's Decision on OPE, slip op. at
52-53), nevertheless, because the issue is the washout period, in this
instance I will accept Dr. Denton's testimony regarding the
administration of Mellaril. Specifically, I will accept that Mellaril
was discontinued 10 days prior to the commencement of the Rao study. I
find that this is probably sufficient for the purposes of including
this patient in the study, although the protocol required a 21-day
washout period. (See G-14.2 at 243.)
Notwithstanding my finding regarding the inclusion of Patient No.
45 despite this patient's use of Mellaril, I note both the violation of
the protocol's 21-day washout period, and the incompleteness of the
records regarding Patient No. 45's use of Mellaril can be considered in
evaluating the adequacy of the Rao study.
As for the administration of Peritrate to Patient No. 45, I note
that the administration of this vasodilating agent was a violation of
specific prohibitions of the protocol against the use of vasodilating
agents other than Cyclospasmol. (G-28.8 at 318.) However,
because Peritrate was not administered near the time of either the
initial evaluation, on January 5, or the final evaluation, on April 8,
I will accept Dr. Denton's estimation that this level of Peritrate was
not a basis to exclude this patient, although I do not accept his
characterization of the use of this drug as ``irrelevant.'' Therefore,
I find that this patient could be included in the analysis of the Rao
study. Nevertheless, this is a clear protocol violation, and the
possible confounding effect of Peritrate should be weighed in reviewing
the adequacy of the Rao study.
Regarding Patient No. 57, Dr. Denton testified that this patient
received Compazine for 2 days during the course of the study. (Denton,
A-121 at 84.) However, I have reviewed the records for this patient,
and I found that the physician's order sheet indicates that Compazine,
10 mg PRN, was ordered on January 30, 1976, with the order running
through February 20, 1976. (G-14.8 at 135.) A second order to
discontinue the Compazine was entered on February 20, 1976. (G-14.8 at
136.) There were no medication records tracking actual administration
of Compazine. I note that this patient's initial evaluation was on
January 30 (G-14.8 at 132), and the patient's final evaluation was on
May 11, 1976. (G-14.8 at 131.)
The Center's argument pertaining to Patient No. 57's concomitant
medication use is based on Dr. Denton's testimony that this patient
received Compazine twice during the study. Because this was the focus
of the Center's argument, I will address my ruling to the Center's
argument, rather than considering the standing order for Compazine
reflected in the patient's records. On this basis, I do not find that
Patient No. 57 needed to be excluded.
Notwithstanding my ruling regarding Patient No. 57's receiving
Compazine, I nevertheless note that AHP's failure to provide
documentation of the administration of Compazine can be considered as a
flaw in the Rao study. (Commissioner's Decision on OPE, slip op. at 52-
53.) While Dr. Denton testified that Compazine was only administered
twice, the physician's order sheets for this patient suggest that this
drug might have been administered more frequently. Because of the
absence of adequate records, this patient's concomitant medication use
can not be fully reviewed, and this fact can be considered in weighing
the adequacy of this study.
The Center also argues that several patients were in violation of
the protocol's 21-day, prestudy washout requirement. (Center Post-
Hearing Brief at Attachment B.) It is alleged that a number of patients
received major tranquilizers during the washout period. However, before
I review the records of each of the patients which the Center cites, I
note that administration of occasional doses of a major tranquilizer
during the study were permitted by the protocol. (G-28.8 at 318).
Because occasional doses were permitted during the study, by extension,
I find that occasional administration of a major tranquilizer might be
said to have been permitted during the prestudy washout period.
However, I also find that the same restrictions on the level of the
dose and the timing of administration, i.e., not within 4 days of an
evaluation, would still apply during the washout period.
Turning now to the Center's arguments, first, the Center argues
that Patient No. 2 received Mellaril during the washout period.
(Denton, A-121 at 72-74.) The problem with assessing Patient No. 2's
use of Mellaril is that this patient's records reveal only that
Mellaril, dose unspecified, was discontinued at the same time that
Cyclospasmol was begun. (G-14.5 at 55.) The record of
Mellaril use during the washout period is not included in the
evidentiary record.
Dr. Leber, a witness for the Center, had testified regarding the
effects of Mellaril. Dr. Leber testified that Mellaril, an
anticholinergic,
[[Page 64124]]
antipsychotic drug, has a great potential to adversely affect
cognition, learning, and memory. (Leber, Tr. Vol. I at 68-69.) Patients
who are receiving Mellaril can have their cognitive performance appear
worse than it actually would have been, absent Mellaril. When the
patient is withdrawn from Mellaril, the patient's cognitive performance
may improve due to the withdrawal of Mellaril. (Leber, Tr. Vol. I at
69.) Moreover, Mellaril is a drug with a ``very long half-life.''
(Leber, Tr. Vol. I at 70.) That is to say, it can accumulate in the
body. (Leber, Tr. Vol. I at 70.)
As for the administration of Mellaril to Patient No. 2, I find this
to be an apparent violation of the protocol's restriction against
giving a patient a major tranquilizer within 4 days of an evaluation,
in this instance the initial evaluation. (G-28.8 at 318.) I use the
word ``apparent,'' since the necessary records of Mellaril use are not
in evidence. However, as was held in the Commissioner's Decision on
OPE, the use of concomitant medication can be considered as ``a fatal
flaw'' in the absence of detailed records which would permit evaluation
of the effect of the concomitant medication on the results of the
study. (Commissioner's Decision on OPE, slip op. at 52-53.) Without the
necessary records regarding Patient No. 2, I find that this patient
should have been excluded from the Rao study.
The Center next argues that Patient No. 51 also received Mellaril
during the washout period. (Center Post-Hearing Brief at Attachment B.)
I have reviewed this patient's medication charts, and I have found that
these records indicate that this patient received Mellaril, 25 mg four
times a day, from December 4, 1975, to January 31, 1976, a time period
which included the entire washout period. (G-14.8 at 40, 41.) This
patient began receiving the study drug on January 30, 1976. (G-14.8 at
40; Leber, G-64 at 14.) Dr. Denton, in his review of this patient's
records, wrote, ``There is no practical necessity of the 3 week
washout, when the final evaluation is done 3 months after the start of
the study.'' (Denton, A-121 at 83.) Dr. Denton, however, did not
address himself to the fact that the initial evaluation of this patient
may have been affected by the frequent and regular use of Mellaril.
The level of Mellaril used by Patient No. 51 was a violation of two
provisions of the protocol. Specifically, this patient received more
than three doses of a major tranquilizer in 1 week, and received a
major tranquilizer within 4 days of initial evaluation. (G-28.8 at
318.) In fact, records support a finding that Mellaril was administered
four times a day even on the day of initial evaluation. I find this
level of Mellaril use by Patient No. 51 at the time of initial
evaluation to be a basis for excluding this patient from the study.
Patient No. 10 received Valium during the washout period. (Denton,
A-121 at 75.) In my review of this patient's records, I found that the
physician order sheets contained a notation which read, ``Valium 5 mg
at 8 PM,'' with the further notation that the medication was to start
on December 11, 1975, and continue until January 19, 1976. (G-14.5 at
233.) However, a later notation indicated that Valium was discontinued
on December 23, 1975, two weeks after it had been initiated. (G-14.5 at
234.) This patient had begun to receive the study drug on December 18,
1975. (G-14.5 at 233.) The administration of Valium to this patient
violated the protocol's general prohibition against the use of
psychoactive drugs except for bedtime use of Noludar or chloral
hydrate. (G-28.8 at 318.) However, I do not find this level of use of
Valium to be cause to exclude this patient. Nevertheless, I note the
fact that this protocol violation can be weighed in evaluating the
adequacy of the Rao study.
Patient No. 14 received Valium, 2 mg twice a day, beginning on
December 15, 1975. (G-14.5 at 334; Denton, A-121 at 77.) This patient
started on the study drug on December 19, 1975; Valium was discontinued
on December 23, 1975. (G-14.5 at 334.) As with the previously discussed
patient, the administration of Valium to Patient No. 14 violated the
protocol's general prohibition against the use of psychoactive drugs
except for bedtime use of Noludar or chloral hydrate. (G-28.8 at 318.)
Nevertheless, I do not find this level of use of Valium to be cause to
exclude this patient, but I note the fact of this protocol violation
can be weighed in evaluating the adequacy of the Rao study.
Also cited by the Center for receiving medications during the
washout period, in addition to the Center's claims of concomitant
medication use during the study by these particular patients, were
Patients No. 22 for receiving Mellaril (Leber, G-64 at 12), Patient No.
29 for receiving both Doxepin, an antidepressant, and Mellaril (Leber,
G-64 at 13), and Patient No. 56 for receiving Valium (Leber, G-64 at
14) during the washout period. I need not discuss these three patients
because AHP has conceded that these patients should be excluded for
violations of the inclusion/exclusion criteria. (See sections
I.D.1.c.2. (regarding Patient No. 22), I.D.1.c.3. (regarding Patient
No. 29), and I.D.1.c.4. (regarding Patient No. 56).)
In summary, the Center had alleged concomitant medication use in
violation of the protocol by 21 of the 58 patients in the Rao study. Of
these 21 patients, AHP has already conceded that 9 patients (Patient
Nos. 9, 22, 23, 29, 32, 36, 43, 56, 68) should be excluded for
violation of the inclusion/exclusion criteria. Additionally, it was
conceded by Dr. Denton, AHP's witness reviewing the Rao study, that
Patient No. 36 should be excluded for the concomitant use of Seconal at
the time of final evaluation.
After these conceded exclusions, there remained 12 other patients
cited by the Center for concomitant medication use, but whose exclusion
AHP contests. Of these patients, I have found that Patient Nos. 1, 2,
6, 17, 28, and 51 should be excluded for concomitant medication use. I
further find that Patient Nos. 10, 14, 42, 45 and 57 can be included,
but that for the various reasons previously discussed, the inclusion of
these patients can be weighed against problems with the records for
these patients, and with the fact that protocol violations were found
in connection with these patients. I note that even protocol violations
which individually may not warrant rejection of a study can be
considered in the aggregate in determining whether a study is adequate
and well-controlled. (See Commissioner's Decision on Benylin, 44 FR
51512 at 51531.) Lastly, I find that Patient No. 24 can be included.
e. Case Report Forms. AHP further makes a general challenge to the
ALJ's consideration of the lack of case report forms for 55 out of the
58 patients as another factor to be weighed in reviewing the adequacy
of the Rao study. (AHP Exceptions at 137-39, citing I.D. at 40, 42.)
AHP argues that the case report forms were not needed because hospital
records (see G-14.5; G-14.6; G-14.7; G-14.8) and computer printouts
(see G-11.2) regarding most of the patients were available. (AHP
Exceptions at 139.)
The Center argues that the case report forms were needed for
several reasons. (Center Response to AHP Exceptions at 53; Center Post-
Hearing Brief at 60-62, 65-66, 68-74.) The Center argues that for most
of the patients, there are no results for the neurological examination
required by the protocol, the absence of which undermines any
assurances by AHP that the patients did not have a neurological cause
for their senility. (Center Post-Hearing Brief at 61-62.) Additionally,
there were no hospital records available for two of the
[[Page 64125]]
patients--Nos. 7 and 48--included in the analysis. (Center Post-Hearing
Brief at 65-66.) For these reasons, it was impossible to determine
whether these patients were given concomitant medications to any
extent. (Center Post-Hearing Brief at 65-66.)
Regarding the computer printouts, the Center argues that these
documents are inadequate because they do not contain necessary
information such as the results of the physical examination, the
neurological examination, and the laboratory tests. (Center Post-
Hearing Brief at 70-72.) Moreover, the Center argues that computer
printouts are not an adequate supplement because the printouts do not
record any of the subjects' medical histories, concomitant medication
use, the SCAG evaluations for ten of the placebo patients, nor the
identities of investigators who made each patient's SCAG evaluation.
(Id. at 70-73.)
Dr. Mohs, a witness for the Center, explained the reasons for
needing the case report forms as follows:
(I)t makes it very difficult to evaluate the study when the
original data forms are not available. It is difficult to determine
how well the records were kept and whether or not there were errors
made in taking the data from the original case report forms to the
analysis system. In other words, it makes it impossible to verify
whether the protocol was followed and whether the results, which
were eventually reported in the published article, accurately
reflect the data that were collected.
(Mohs, G-62 at 8.)
Similar testimony was given by Dr. Leber, a witness for the Center,
who testified in part, ``The documentation supplied by the sponsor
(makes) it impossible to determine whether or not certain requirements
of the protocol were actually carried out.'' (Leber, G-64 at 16.)
The act requires that a new drug application include ``full reports
of investigations'' which have been made to show whether such drug is
effective in use. (21 U.S.C. 355(b)(1).) This statutory requirement was
extensively discussed in the Commissioner's Decision on OPE. In that
decision, it was noted that neither the statute nor agency regulations
imposes a per se requirement that in every instance raw data be
submitted in support of a new drug application. (Commissioner's
Decision on OPE, slip op. at 66.) The Commissioner's decision on OPE
went on to note that while raw data are not required in support of all
NDAs, this does not mean, however, that the submission of raw data may
never be required by the agency. The ``full reports'' requirement can
be met without access to the raw data only when the report of the
study: (1) Is published in the scientific literature, (2) is reliable,
and (3) describes an adequate and well-controlled study.
(Commissioner's Decision on OPE, slip op. at 67.)
Additionally, it should be noted that publication alone does not
negate the necessity for raw data from a study to be supplied to the
agency. Regarding published studies, the Commissioner's Decision on OPE
ruled:
(P)ublished studies can be considered reliable and can be
accepted without supporting raw data only if the reports of the
studies contain details adequate to support a scientific
determination that the study is an adequate and well-controlled
clinical investigation. The determination of whether the report is
adequate (and raw data unneeded) is a discretionary determination
made on the basis of the quality of the published data. Among the
factors that determine whether a published report is sufficient are
whether the protocol, the results, and the manner by which the study
meets each of the requirements of (FDA regulations) are described in
detail.
(Commissioner's Decision on OPE, slip op. at 70-71 (citations omitted,
emphasis added).)
Turning now to the Rao study, I note that while the Rao study was
published in the Journal of the American Geriatrics Society, the
article, which was four pages in length, failed to provide any details
regarding the patient selection process, and completely failed to
discuss concomitant medication use, and further failed to discuss
concomitant diseases or conditions which the patients had during the
course of the study. (A-80 at 1-4.) The computer printouts which AHP
cites are not sufficient to make up this deficit because the printouts
do not contain information such as the results of the neurological
examination required by the protocol, nor do the printouts identify
which doctor performed which SCAG evaluation. (I.D. at 39.) The
hospital records, which do not contain SCAG or NOSIE scores but which
do contain information regarding concomitant medication use, are
missing for two of the patients included in the analysis. (Center Post-
Hearing Brief at 65.)
I find that Dr. Rao's published report fails to contain details
adequate to support the scientific determination necessary to find that
the Rao study is an adequate and well-controlled clinical
investigation. Therefore, I find that the unavailability of the raw
data was a matter properly considered by the ALJ. I conclude that the
omission of the raw data can be weighed in determining whether the Rao
study was adequate and well-controlled.
f. Blinding and bias. Regarding the matter of bias, the Center
argues that Dr. Rao did not remain blinded throughout the clinical
trial and for this reason was biased in his observations. (Center Post-
Hearing Brief at 75; Center Response to AHP Exceptions at 53-54.) AHP
argues that the evidence fails to support the Center's claims. (AHP
Post-Hearing Brief at 99-104; AHP Exceptions at 142-47.) While the ALJ
discussed the issues of bias and blinding in the Initial Decision, the
ALJ made no ruling regarding this matter. (I.D. at 41-42, 43.)
Dr. Rao had died prior to the commencement of the administrative
hearing, so there was no direct testimony from him on this point. The
underlying basis for the Center's claims lies in the fact that of the
16 Cyclospasmol-treated subjects assigned to Dr. Rao, Dr. Rao
rated 10 of these subjects as ``markedly improved,'' whereas the three
other investigators in the same study (Drs. Georgiev, Guzman and Paul),
who together rated 16 Cyclospasmol-treated subjects, only
rated one subject as ``markedly improved.'' (Mohs, G-62 at 12-13; Thal,
G-63 at 8, citing (G)-11.2 at 72-73 & (G)-14.2 at 254; Leber, G-64 at
18.) The Center argues that this disparity in ratings among the four
evaluators indicates that adequate measures were not taken to minimize
bias on the part of the observers and analysts of the data. (Center
Response to AHP Exceptions at 53-54.)
In support of its argument on the blindness issue, the Center cites
to the testimony of three of its witnesses--Drs. Leber, Thal, and Mohs.
(Center Post-Hearing Brief at 75.) Each of these witnesses raised
questions about the credibility of Dr. Rao's ratings as compared with
that of the three other investigators in the Rao study.
On this issue, Dr. Leber, a witness for the Center, testified that
there was ``a marked inconsistency between (Dr.) Rao's findings and
those of his three co-investigators.'' (G-64 at 18.) Dr. Leber noted
that of the 32 patients collectively assigned to the four investigators
in the Cyclospasmol arm, 12 of the 13 patients reported to
have shown the largest improvements from baseline on SCAG Item 19 were
in Dr. Rao's group. (G-64 at 18.) Additionally, Dr. Leber testified
that on the physician's final global evaluation of each patient, a
``marked improvement,'' the highest level of improvement, was reported
by all investigators for 11 of the 32 patients in the
Cyclospasmol arm, with 10 of these 11 ``marked improvements''
being reported by Dr. Rao. (G-64 at 18.) Dr.
[[Page 64126]]
Leber added that the hospital records often failed to support the
marked improvements which Dr. Rao reported. (G-64 at 20.) Dr. Leber
expressed the view that ``at best, Dr. Rao's use of the SCAG represents
a sort of `grade inflation.' That is, patients who have either had only
trivial or minimal changes are rated as having very large
improvements.'' (G-64 at 20.)
Dr. Leber also cited numerous specific examples of patient
evaluations which he found to be questionable. (G-64 at 20-22.) Among
the patients cited by Dr. Leber were Patient Nos. 15, 17, 20, 29, and
63. All of these patients were reported by Dr. Rao to have had a 3.0
change on SCAG Item 19, yet the clinical psychologist reports for the
Rao study indicated that these patients worsened during the study. (G-
64 at 20-22.) Other patients, including Patient Nos. 16, 22, 24, 52,
and 56 were also reported by Dr. Rao to have had an improvement in
their SCAG scores by 3.0 points, and, in one instance, a 4.0
improvement, yet the clinical psychologist evaluation reported no
change in these patients or, in the case of the patient with the
reported 4.0 change, minimal improvement. (Leber, G-64 at 21-22.)
Dr. Thal, another witness for the Center, similarly expressed the
view that there were a number of items that suggested a ``credibility
gap'' in the Rao study. (Thal, G-63 at 8.) On this point, Dr. Thal
testified:
First, although 4 different investigators rated the patients,
only Dr. Rao found a large number of markedly improved patients. * *
* The second problem is that Dr. Rao's global improvement evaluation
of marked improvement in the 10 patients is not substantiated by
other observers (including NOSIE scores, clinical psychology notes,
nursing notes, and doctors' progress notes.) Overall, the
discrepancies noted raise questions about the credibility of the
data.
(Thal, G-63 at 8.)
Regarding this issue, Dr. Richard C. Mohs similarly testified:
Since (Dr. Rao) evaluated only 16 patients in this group (the
Cyclospasmol arm) Dr. Rao rated 62% of his
Cyclospasmol patients as markedly improved while the other
three physicians together only rated 1 of 16 patients as markedly
improved (6%). This is very unlikely to have occurred by chance and
suggests that Dr. Rao may not have been blind to the drug conditions
of the patients.
(Mohs, G-62 at 13.)
I have reviewed the evidence cited by the Center in support of its
argument, but I do not find the evidence sufficient to support the
serious charge that Dr. Rao became unblinded during the clinical trial
and failed to report becoming unblinded. While the evidence does seem
to indicate a sort of ``grade inflation'' on Dr. Rao's part, as was
suggested by Dr. Leber in his testimony, nevertheless the evidence is
inconclusive regarding the question of Dr. Rao's blinding. There is no
evidence which I find which is dispositive of the Center's claim of
unblinding by Dr. Rao. Moreover, there is no evidence which indicates
that Dr. Rao's patients were randomized between placebo and
Cyclospasmol arms in a way different from that of the
patients in other investigators' groups, which might have revealed the
patient's status to Dr. Rao. I find that while the disparity in ratings
among the investigators was an issue properly raised by the Center,
nevertheless I find the evidence ambiguous and not sufficient to
support the Center's claim. Therefore, I rule in favor of AHP on the
issues of blinding and bias.
g. Adequacy of the Rao study. In sum, I find that the Rao study was
not adequate and well-controlled. In making this determination, I have
considered the aggregate effect of the protocol violations. As I
previously discussed: (1) The study failed to show that patients were
examined for other causes of dementia, and therefore the study did not
adequately show that Alzheimer's disease patients were included in the
study; (2) patients with concomitant diseases and conditions, including
strokes, histories of alcoholism, severe diabetes, Parkinson's disease,
and other serious diseases were admitted to the study, although these
patients were to have been excluded under the protocol; and (3) the
widespread administration of concomitant medications precluded any
meaningful analysis of the effects of Cyclospasmol in the
study. Also, I find that Dr. Rao's published report failed to contain
details adequate to support the scientific determination that the Rao
study is an adequate and well-controlled clinical investigation; the
unavailability of the raw data was a matter properly considered by the
ALJ, and the omission of the raw data can be weighed in determining
whether the Rao study was adequate and well-controlled. I further find
that the ALJ did not err in refusing to admit AHP's reanalysis of the
Rao study, since the reanalysis was not timely filed and AHP did not
make a motion justifying the potential delay resulting from the
document's late submission. I did rule in favor of AHP on the issue of
the blinding and bias of Dr. Rao. However, the favorable ruling on this
issue is not enough to counteract the aggregate effect of the other
deficiencies of the Rao study.
2. The Yesavage Study
The Yesavage study was originally planned as a multicenter study
combining the results of three investigators at three different sites.
However, the results of one of these investigators were dropped at the
request of FDA because of certain questions about that portion of the
study. (I.D. at 43; see also G-10.2 at 1-2.) The results of the second
investigator were not submitted by AHP, for reasons which are disputed
by the Center but which are not at issue in this appeal. (I.D. at 43-
44.) In any case, only the results of Dr. Yesavage's group were
submitted as proof of efficacy for Cyclospasmol. Hereinafter,
the results of Dr. Yesavage's group will be referred to as the Yesavage
study.
The Yesavage study was a placebo-controlled, parallel group study
with the stated objective of evaluating ``the efficacy of
Cyclospasmol compared to placebo in improving symptoms
usually associated with impaired brain function in the elderly, whether
due to cerebral arterial disease or diffuse cellular dysfunction.'' (G-
9.2 at 32.) Twenty-eight patients were enrolled at the start of the
study. (I.D. at 43, citing G-9.2 at 32; G-11.1 at 10, 17.)
Under the protocol, patients selected for the Yesavage study were
to be ``residing in a retirement, intermediate care facility,
convalescent, nursing or other home for the aged and who exhibit mild
to moderate deterioration of brain function as manifested by their
behavior or symptoms * * *.'' (G-9.2 at 32.) Accordingly, the patients
selected for the study were drawn from one of three nursing homes and
from an intermediate care facility (Lincoln Glen Manor, Empress
Convalescent Hospital, Skyline Convalescent Hospital, or Lincoln Glen
Intermediate Care Facility). (I.D. at 43, citing Yesavage, Tr. IV at
43-44.) However, a few patients lived at home with relatives. (I.D. at
43, 46; Yesavage, Tr. Vol. IV at 43-44.)
Subjects in the study were assessed on the basis of 28 outcome
measures. These measures included the Nurses Observation Scale--
Inpatient Evaluation (NOSIE), which, in contrast to the NOSIE in the
Rao study, was used to give a single measure for each patient, the
Hamilton Depression Scale, the Buschke Memory Test (BMT), the
physician's clinical global impression score, and the 24 measures--5
factors plus 19 items--on the Sandoz Clinical Assessment--Geriatric
(SCAG). (G-9.2 at 45.)
At time of final analysis, the results of 23 of the 28 patients in
the study were analyzed on the basis of measurements
[[Page 64127]]
taken at Weeks 3, 6, 9, and 12. (I.D. at 43, citing G-64 at 24; see
also G-11.1 at 17.) However, additional and variable numbers of
patients were excluded from the final analysis for which the patients'
baselines were compared with their outcomes at Week 16, which was the
final week of the study. (G-11.1 at 20-37.) For the SCAG rating, 20
patients, including 12 Cyclospasmol and 8 placebo patients,
were used. (G-11.1 at 29-31.) For the BMT, the results of 17 patients,
including 10 Cyclospasmol and 7 placebo patients, were
analyzed. (G-11.1 at 32.) For the Clinical Global Impression, the
measures of 22 patients, of which 13 were Cyclospasmol
patients and 9 were placebo patients, were used. (G-11.1 at 33.) For
the NOSIE scale, 15 patients, including 10 Cyclospasmol and 5
placebo patients, were used. (G-11.1 at 34-36.) For the Hamilton
Depression Scale, 21 patients, including 13 Cyclospasmol and
8 placebo patients, were analyzed. (G-11.1 at 37.) AHP's reasons for
analyzing different numbers of patients for each outcome measure were
not discussed in the final analysis of the Yesavage study. (See G-11.1
at 5- 45.)
Based upon the results of the 20 patients whose outcomes were
included in the final analysis of the SCAG Factors, AHP reported a
statistically significant difference in favor of Cyclospasmol
on SCAG Factor 1 (``cognitive dysfunction''), and SCAG Item 19
(``overall impression of patient functional capacity''). (G-11.1 at 19-
20, 29, 78; Thal, G-63 at 16-17; Chaing, Tr. Vol. I at 52-53; Overall,
A-116 at 6.)
The ALJ ruled that the Yesavage study cannot be considered an
adequate and well-controlled study, in part, because: (1) Patients who
did not meet the entrance criteria were included in the study, (2)
concomitant medication use confounded the study, and (3) clinical
significance was not demonstrated. AHP and the Center make the
following arguments challenging the ALJ's decision.
a. Selection of patients.--(i) Parkinson's Disease. AHP first
argues that the ALJ erred in ruling that two of the patients in the
study--Patient Nos. 34 and 37--had Parkinson's disease and should have
been excluded. (AHP Exceptions at 149, citing I.D. at 53, 57.) AHP
argues that this ruling is an error because the protocol for the
Yesavage study did not exclude patients with Parkinson's disease. (AHP
Exceptions at 149.)
The Center argues that these two patients should properly be
excluded because Parkinson's disease itself causes dementia, which
could confound the results of the study. (Center Response to AHP
Exceptions at 55-57.) The Center additionally argues that Parkinson's
disease is a type of organic brain syndrome (Denton, Tr. Vol. VII at
38), and that patients with organic brain syndrome were to have been
excluded under the Yesavage protocol's exclusionary criteria. (Center
Response to AHP Exceptions at 56 n.26, citing G-9.2 at 34.)
Whether the inclusion or exclusion of a particular patient is
consistent with the protocol is one factor which can be considered in
reviewing a study, for it goes towards proving whether the study was
adequate and well-controlled. However, conformance to a study's
protocol is not an ironclad guarantee that the study will be found to
be adequate and well-controlled.
The burden of designing and conducting an adequate and well-
controlled study lies with the proponent of the drug. (Commissioner's
Decision on Mysteclin, slip op. at 11; see generally Sec. 314.126.)
Protocols can be found to be inadequate. If a protocol is flawed, it
does not matter if the protocol was perfectly adhered to in its
execution. (Cf. Commissioner's Decision on Cothyrobal, 42 FR 28602 at
28604 and 28606 (Study found not to be adequate and well-controlled
because design of study did not include test arms for all components of
a combination drug.).) Moreover, FDA cannot be estopped in its review
of safety and effectiveness issues. (United States v. Articles of Drug
* * * Hormonin, 498 F. Supp. 424, 437 (D.N.J. 1980), aff'd 672 F.2d 904
(3d Cir. 1981).)
Turning now to the evidence regarding the Yesavage study, the
record shows that Dr. Leon Thal, a witness for the Center, testified
that Parkinson's disease can cause dementia. (Thal, G-63 at 12.)
Specifically, Dr. Thal testified, ``Patients with Parkinson's disease
do have dementia, however, the dementia may not be secondary to
Alzheimer's disease but due to a dementia associated with Parkinson's
disease which has a different pathological basis.'' (Thal, G-63 at 12.)
FDA regulations require that a protocol for an adequate and well-
controlled study have a ``method of selection of subjects (that)
provides adequate assurance that they have the disease or condition
being studied * * *.'' (Sec. 314.126(b)(3).) In the Commissioner's
Decision on Lutrexin it was ruled, under an earlier edition of the
regulations, that it is necessary to use ``the most accurate diagnostic
techniques available'' to assure that patients who do not have the
condition under study are identified and excluded from the study; the
failure to do so ``undermin(es) the validity of the results.'' (41 FR
14406 at 14419.)
Having reviewed the Yesavage study, I find that the ALJ was correct
in ruling that Parkinson's disease, though not specifically excluded by
the protocol, would make it more difficult to characterize the
improvement of a demented patient. (I.D. at 45.) I conclude that
because dementia caused by Parkinson's disease is not a labeled
indication for Cyclospasmol, Patient Nos. 34 and 37, who had
Parkinson's disease, should have been excluded from the study to
prevent confounding of the study's results.
The record also supports a finding that Patient No. 18 had
Parkinson's disease. Patient No. 18's case record states that this
patient had ``Parkinsonian tremor.'' (G-12.4 at 108.) Additionally,
testimony indicates that this patient received the drug, Sinemet,
during the study. Sinemet is used in the treatment of Parkinson's
disease. (Denton, A-121 at 54.)
While the ALJ noted that the evidence indicated that Patient No. 18
had Parkinson's disease, the ALJ declined to rule that this patient
should have been excluded for having Parkinson's disease because the
Center failed to make this argument. (I.D. at B-2.) In view of the
ALJ's ruling on this matter, I, too, will refrain from ruling that
Patient No. 18 should be excluded despite the evidence of Parkinson's
disease. Nevertheless, I rule that AHP's failure to address this
patient's apparent concurrent condition can be considered in the
weighing of the Yesavage study.
ii. Outpatients. AHP further argues that the ALJ erred in ruling
that three other patients--Patients Nos. 14, 16, and 18--should have
been excluded from the study because these patients lived at home with
their families, rather than in a nursing home as required by the
protocol. (AHP Exceptions at 152, citing I.D. at 46.) AHP argues that
the inclusion of these patients represented mere technical violations
of the protocol, and that these patients need not have been excluded.
The relevant section of the Yesavage study protocol provided that
subjects for the study shall be ``(p)atients who are residing in a
retirement, intermediate care facility, convalescent, nursing home or
other home for the aged * * *.'' (G-9.2 at 32.) While the purpose for
this requirement is not stated in the protocol, the ALJ, after hearing
all the evidence, concluded that the purpose of this requirement was to
assure that patients were taking the study medication as directed, and
to assure that the use of concomitant medication would be monitored.
(I.D. at
[[Page 64128]]
46; AHP Exceptions at 152; see generally Porter, Tr. Vol. IV at 43-46.)
The ALJ's conclusions on this point are not in dispute.
While the ALJ made a ruling regarding three of the study subjects,
I note that testimony from Dr. Clarence Denton, an AHP witness,
indicates that five patients--Patient Nos. 14, 15, 16, 17, and 18--were
outpatients. (Denton, A-121 at 48.) However, the evidence in the record
does not include the case reports for Patient Nos. 15 and 17. Perhaps
for this reason, the ALJ mentions only Patient Nos. 14, 16, and 18 in
his decision. (See I.D. at 46.) However, I conclude that the
testimonial evidence of Dr. Denton is a sufficient basis for reviewing
the status of all five of the outpatients.
Dr. Yesavage testified that the patients who lived at home were
seen by Dr. William Garcia in the latter's private office, although Dr.
Yesavage was listed on the case report forms as the patients' doctor.
(Yesavage, Tr. Vol. IV at 43, 46.) Dr. Yesavage testified that Dr.
Garcia was not required by the protocol to record concomitant
medications into the case report forms. (Yesavage, Tr. Vol. IV at 45.)
For nursing home patients, concomitant medications were noted on the
patient order sheets; regarding outpatients, Dr. Yesavage testified
that he ``presume(d)'' that Dr. Garcia made notes in his private files
regarding concomitant medications for the outpatients. (Yesavage, Tr.
Vol. IV at 44-46.)
The responsibility of recording all subjects' concomitant
medications, including that of the outpatients, onto the case report
forms was given to Mr. Michael Adey, Dr. Yesavage's assistant.
(Yesavage, Tr. Vol. IV at 45-46.) For the nursing home patients, it was
Mr. Adey's responsibility to review the order sheets, identify
concomitant medications, and record these into the case report forms.
(Yesavage, Tr. Vol. IV at 47.) For the outpatients, Mr. Adey was
similarly to review the medical records from Dr. Garcia, identify
concomitant medications, and record this information into the case
report forms. (Yesavage, Tr. Vol. IV. at 48.)
The Center argues that the outpatients should properly be excluded
because there is no evidence to show that the families of the
outpatients kept careful records of any concomitant medications given
at home, nor does the evidence show that Mr. Adey recorded in the case
report forms concomitant medications given at home. (Center Response to
AHP Exceptions at 59.) Additionally, the Center argues that there is no
evidence that the outpatients' families kept careful records regarding
the administration of the test drug. (Center Response to AHP Exceptions
at 59.)
FDA regulations require that a study use a design ``that permits a
valid comparison with a control to provide a quantitative assessment of
drug effect.'' (Sec. 314.126(b)(2).) The regulations also require that
``(t)he method of assigning patients to treatment and control groups
minimize bias and * * * assure comparability of the groups with respect
to pertinent variables such as * * * use of drugs or therapy other than
the test drug.'' (Sec. 314.126(b)(4).) Monitoring a patient's
medications during the course of a study is an important factor in the
design of an adequate and well-controlled study and is necessary for a
valid comparison between a test article and a control. (See generally
Commissioner's Decision on OPE, slip op. at 47-53.)
While restricting the Yesavage study to patients who were in a
nursing home and under constant medical supervision is one way to
monitor concomitant medications, this restriction is not perforce
required to monitor concomitant medications. Although the evidence
indicated that there were problems with recording of concomitant
medications \6\ and with concomitant medication use (the latter of
which will be discussed in section I.D.2.d. of this document), these
problems do not appear to be unique to the outpatients in the Yesavage
study. For these reasons, I will accept AHP's argument that the
inclusion of outpatients was a technical violation of the protocol and
was not grounds by itself to exclude these patients.
---------------------------------------------------------------------------
\6\ Dr. Yesavage testified that his research assistant may not
have included all sleeping medications in the case report records of
concomitant medications. (Yesavage, Tr. Vol. IV at 42.) Dr. Yesavage
explained that his research assistant was permitted to ``use some
judgment'' in deciding which medications to include on the case
report forms because it was not felt that it was important to
include all concomitant medications regardless of their indications.
(Yesavage, Tr. Vol. IV at 42.)
---------------------------------------------------------------------------
Nevertheless, as I previously noted, even protocol violations which
by themselves may not warrant rejection of a study can be considered in
the aggregate in determining whether a study is adequate and well-
controlled. (See Commissioner's Decision on Benylin, 44 FR 51512 at
51531.) Failure to follow inclusion/exclusion criteria can be an
indication of an inattention to detail and can be considered in
deciding whether the study was adequate and well-controlled.
Therefore, I find with respect to the Yesavage study that the
inclusion of outpatients in violation of the study's protocol may be
considered in evaluating the adequacy of the Yesavage study.
b. Distribution of patients with strokes. Unlike the Rao study's
protocol, which planned to exclude patients with strokes, the Yesavage
study's protocol did not propose to exclude stroke patients. This
difference between the two studies' protocols was not an issue at the
administrative hearing.
AHP argues that the ALJ erred in holding that seven patients in the
Yesavage study had medical histories indicating strokes, and that these
patients should have been proportionately distributed between the drug
and placebo groups. (AHP Exceptions at 154, citing I.D. at 53, 57.) The
Center, citing to the testimony of Dr. Thal, argues that AHP's failure
to identify patients with stroke histories and to see that such
patients were proportionately assigned between the Cyclospasmol
and the placebo groups meant that the two groups cannot be
found to be comparable. (Center Response to AHP Exceptions at 60-61.) I
find the Center's argument to have merit.
Turning first to the testimony of Dr. Thal, a witness for the
Center, this witness testified:
There are some problems with the protocol in that the protocol
does not attempt to separate out patients who have Alzheimer's
disease from those who had multiple strokes. A problem with lumping
together two groups of patients is that if they are unequally
distributed, the treatment effect seen may be due to an effect on
the treatment on one disorder and not the other. For example, if a
large number of patients with multiple strokes are in the treatment
group, the effect of the drug would then be licensed for the
treatment of both patients with multi-infarct dementia and
Alzheimer's disease when in fact the drug may be totally non-
effective in patients with Alzheimer's disease. In reviewing the
case report forms for these patients, I found (7) patients with a
history or an examination compatible with stroke (patients 9, 25,
28, 29, 33, 34, 35). If these patients are removed from the
statistical analysis, it is perfectly possible that all statistical
significance would be lost in the remaining patients.
(Thal, G-63 at 11 (emphasis added).)
I have reviewed the records for all patients in this study, and I
have found that Dr. Thal was correct with regard to six of the seven
patients which Dr. Thal identified as having histories of strokes. I
was unable to verify the diagnosis of a stroke with regard to Patient
No. 25, as there are no records in evidence for this patient. However,
regarding the remaining six patients, the records support Dr. Thal's
testimony. Patient No. 9's records show a clinical diagnosis of a
stroke, specifically a cerebral
[[Page 64129]]
vascular accident with left hemiplegia. (G-12.2 at 106, 109.) Patient
No. 28's records show a diagnosis of a stroke. (G-12.6 at 309, 312-13.)
Patient No. 29's records show a diagnosis of a stroke, specifically a
cerebral vascular accident with right hemiplegia. (G-12.7 at 4, 7-8.)
Patient No. 33's records show a diagnosis of a stroke, specifically a
cerebral vascular accident with left hemiplegia. (G-12.7 at 107, 110-
11.) Patient No. 34's records show a diagnosis of a stroke with left
hemiparesis. (G-12.7 at 210, 215-16.) Patient No. 35's records indicate
a diagnosis of stroke. (G-12.8 at 9.) Additionally, Patient No. 7's
records indicate a diagnosis of a stroke (G-12.2 at 5), although this
patient was not identified by the Center in its brief as a stroke
patient.
What the records do not reveal, either in the patient records or in
the analysis of the Yesavage study, is to which group
(Cyclospasmol or placebo) these, or indeed any, of the
patients were assigned. (See G-12.1 through 12.8; G-11.1.) While AHP
faults the ALJ's decision for failing to make a finding as to how the
stroke patients were distributed, AHP offers no information in this
regard. (AHP Exceptions at 155.)
Based upon the evidence in the record, it cannot be ascertained
whether both arms of the clinical trial included stroke patients. For
this reason, I find that, strictly speaking, proportional distribution
of stroke patients is not the crux of this issue; rather, it is the
failure to show that stroke patients were included in both the
Cyclospasmol arm and the placebo arm of the clinical trial.
As I previously ruled (see section I.D.1.b. of this document), in
an adequate and well-controlled study, it is not acceptable to group
persons having similar symptoms but distinct diseases together into one
study without identifying which patient has which disease, otherwise,
as in the Yesavage study, it will be impossible to assess a drug's
effectiveness on a particular disease. (Cf. Commissioner's Decision on
Lutrexin, 41 FR 14406 at 14422 (In a study of premature labor, results
were ruled incapable of scientific interpretation because women with
different conditions were evaluated together.)) It is, of course,
essential to show that a drug is tested on the population for which it
is labeled. As was ruled in the Commissioner's Decision on Cothyrobal,
``Clearly, a study * * * must be conducted in patients who have one of
the labeled indications if that study is to be used as proof of
effectiveness for those indications.'' (42 FR 28602 at 28610.)
Similarly, in the Commissioner's Decision on Lutrexin, it was ruled,
``(T)he law is clear that the applicant must provide substantial
evidence of a drug's effectiveness under its labeled conditions of use,
not those under which an investigator chooses to test it.'' (41 FR
14406 at 14419.)
The Center cites to the regulation requiring that the method of
assigning subjects must assure comparability of the groups with respect
to pertinent variables, including severity and duration of disease.
(Center Response to AHP Exceptions, citing Sec. 314.126(b)(4); see also
Commissioner's Decision on Lutrexin, 41 FR 14406 at 14414.)
Necessarily, the group assignments must be comparable with respect to
the disease itself. I therefore find that the failure to show that
stroke patients were included in both the drug and the placebo arms of
the clinical trial can be considered as a flaw in the Yesavage study,
and can be weighed in determining if the study was adequate and well-
controlled.
c. Baseline comparability. AHP next argues that the ALJ erred in
finding that the lack of comparability between the drug and placebo
groups at baseline for the Buschke Memory Test (BMT) weighed against
finding the Yesavage study adequate and well-controlled. (AHP
Exceptions at 156-57, citing I.D. at 48, 53, 57.) The average BMT score
at baseline for the Cyclospasmol group was ``7.2'' out of a
possible score of ``15.0,'' but was ``3.6'' for the placebo group, a
difference between the two groups which was statistically significant.
(Schneiderman, G-65 at 10; Thal, G-63 at 13.)
AHP argues that the BMT measured only a narrow parameter of
cognitive functioning, and that the results of other tests at baseline
should have been weighed more heavily. Specifically, AHP cites to the
baseline measures for SCAG Factor 1 (``cognitive dysfunction''), SCAG
Item 3 (``impaired recent memory''), SCAG Item 19 (``overall impression
of patient functional capacity''), the Hamilton Depression Scale, and
the NOSIE, which were comparable at baseline for the drug and placebo
groups. (AHP Exceptions at 158; I.D. at 48.)
The Center concedes that the BMT measures a narrower parameter of
cognitive dysfunction, specifically, recent memory dysfunction, but
argues that impaired recent memory is the core of cognitive dysfunction
and is, therefore, a critical parameter. (Center Post-Hearing Brief at
86, citing Thal, Vol. VI at 45.) The Center further argues that the
BMT's baseline values carry more weight than the SCAG's baseline values
because the BMT is an objective, quantitative test of recent memory
dysfunction. (Center Response to AHP Exceptions at 63.) By contrast,
the SCAG is a subjective, observer-rated test. (Center Post-Hearing
Brief at 86.) The Center argues that for this reason, the BMT is more
telling of baseline comparability between the two study groups. The
Center further argues that the lack of baseline comparability on the
BMT rendered the Yesavage study not adequate and well-controlled.
(Center Reply to AHP Exceptions at 63.)
Before discussing the merits of this issue, the relevant parameters
of the SCAG and the BMT need to be described. The SCAG required the
physician to rate the patient from a list of 19 Items. Each Item in the
SCAG was rated on a scale from ``1'' to ``7,'' with ``1'' indicating
that the symptom was ``not present,'' and ``7'' indicating that the
symptom was ``severe.'' (G-3.1 at 97; see, e.g., G-14.2 at 6-8.)
Eighteen of these Items were then grouped into five Factors for rating
the patient. (G-11.1 at 70.) The 19th Item, the Physician's Overall
Assessment of the patient, was rated separately. (G-11.1 at 70 n.7.)
The Factor upon which AHP now relies, Factor 1, Cognitive Dysfunction,
was defined as including the following Items: (1) Confusion, (2)
impaired mental alertness, (3) impaired recent memory, and (4)
disorientation. (G-11.1 at 70-71, 75.)
The BMT, on the other hand, was described by Dr. Yesavage, an AHP
witness, as ``a memory performance test in which subjects are required
to remember and repeat words from a stimulus list of 15 objects.'' (G-
11.1 at 21.)
Regarding the differences between the SCAG and the BMT, Dr. Thal, a
Center witness, testified:
The SCAG is a subjective measure based on an interviewer rating
scale. The rating scale is such that it is neither objective nor as
accurate as the type of data that one would generate on the Buschke
memory test. Additionally, and more importantly, the SCAG measures
many factors other than memory such as sociability, mood, etc. Only
a small number of the SCAG items deal directly with memory.
(Thal, G-63 at 14.)
The main disagreement between AHP's witnesses and the Center's
witnesses lies in which test the witnesses think should be given more
weight. Dr. Thal testified that he would recommend relying upon the BMT
as an indicator as to whether the two populations were similar,
especially for indications of cognitive dysfunction or memory problems.
(Thal, G-63 at 14.) By contrast, Dr. Klerman, an AHP
[[Page 64130]]
witness, testified that he would give greater weight to the SCAG.
(Klerman, Tr. Vol. III at 87.)
Under FDA regulations, for a clinical trial to be considered
adequate and well-controlled, assignment of patients must be
accomplished by a method that minimizes bias and ``assur(es)
comparability of the groups with respect to pertinent variables such as
* * * severity of disease * * *.'' (Sec. 314.126(4).) With regard to
the Yesavage study, short-term memory loss is one of the
characteristics of senile dementia. Therefore, the severity of the
impairment of recent memory functioning is a pertinent variable in the
evaluation of senile dementia.
While SCAG Item 3 includes impaired recent memory as a
characteristic to be evaluated, SCAG Item 3 is, nevertheless, a
subjective measure. The BMT quantifies the severity of the recent
memory impairment through an objective test of short-term memory. As
such, the BMT is an indicator of the severity of this aspect of senile
dementia. A statistically significant difference between the treatment
and the placebo groups on this measure, with the placebo group being
worse, does indicate a lack of comparability between the treatment and
placebo groups on one of the hallmarks of senile dementia.
Therefore, I find that the statistically significant difference
between the two groups at baseline was a proper consideration to be
weighed in determining whether the Yesavage study was adequate and
well-controlled.
d. Concomitant medications. The law regarding concomitant
medications was discussed in a previous section of this decision, and I
will not repeat it here. (See section I.D.1.d. of this document.)
The Yesavage study protocol contains an extensive section
pertaining to concomitant medications, which in full reads:
Treatment with vasodilating, anti- convulsive, psychoactive, or
narcotic agents, ergot or reserpine derivatives or steroids (other
than estrogen) will not be allowed during this study. The patient
may have chloral hydrate as a hypnotic. Occasional doses of
thioridazine or diazepam may be used if deemed necessary; however,
no more than 16 doses of one of these agents may be taken per study
and there should be no more than three doses in any week. Other
medication, which is considered necessary for the patient's welfare
and which will not interfere with the study medication, may be
continued at the discretion of the investigator, but no new drug,
other than those previously stated, should be started during the
course of this study, except that medication required for an acute
purpose which would not disqualify the patient (e.g., an analgesic,
an antibiotic, etc.). If the investigator feels it is necessary to
start or change a chronic medication during the course of the study,
he will contact the Ives Medical Monitor to determine whether the
patient may continue in the program. However, if during the course
of the study the investigator feels it is necessary to start the
patient on digoxin and/or diuretic therapy because of congestive
heart failure he may do so, without consulting the Ives Medical
Monitor, unless the severity of the congestive heart failure
interferes with the administration of the study drugs or creates a
major change in the patient's mental state. In either of the latter
situations, the patient should be dropped from the study.
Administration of all concomitant medication must be reported on
the case report form, supplied by the sponsor, including the name of
the drug, dose, reason for use and date started.
(G-9.2 at 34-35 (emphasis in original).)
Regarding concomitant medications, the Center identified 12
patients who received 11 different concomitant medications with
possible confounding effects. The patients identified by the Center and
the medications which these patients were said to have taken included
Patient No. 2 (Aldomet, Inderal, Elavil), Patient No. 5 (Inderal,
Valium), Patient No. 7 (Inderal), Patient No. 9 (Dalmane), Patient No.
16 (Sinemet), Patient No. 18 (Sinemet), Patient No. 21 (Mellaril),
Patient No. 24 (Inderal, Serax), Patient No. 33 (Elavil), Patient No.
34 (Benadryl, Phenergan), Patient No. 35 (Haldol), and Patient No. 37
(Elavil, Sinemet). (See Center Post-Hearing Brief at Attachment D.) The
ALJ also identified a 12th concomitant medication, Librium, which was
given to Patient No. 16, who received 10 mg of this drug. (I.D. at B-2;
Denton, A-121 at 52.) AHP does not concede that any of these patients
should be excluded. (AHP Post-Hearing Brief at 108; AHP Exceptions at
163.) The concomitant medication use of each of these patients will be
discussed in turn.
Patient No. 2, who was in the Cyclospasmol group,
received three concomitant drugs during the study, specifically
Aldomet, Inderal, and Elavil. (I.D. at B-1.) Regarding Aldomet, an
antihypertensive drug, Patient No. 2 received 250 mg of this drug three
times a day throughout the study. (G-12.1 at 11, 29, 42, 57, 60, 63,
70.) Aldomet can affect mood and cognition. (Leber, G-64 at 13.)
Additionally, according to the testimony of Dr. Denton, a witness
for AHP, Patient No. 2 received 40 mg of Inderal twice a day throughout
the study. (Denton, A-121 at 52-53.) This patient's case records do not
document the administration of Inderal to this patient. (See G-12.1 at
4-105.) Regarding Inderal, Dr. Denton testified that Inderal in ``a
large dose, perhaps more than 80 mg/day, might make patients confused
or depressed.'' (Denton, A-121 at 53.) Other possible side effects of
Inderal include disorientation, short term memory loss, clouded
sensorium, and decreased performance on neuropsychometric tests.
(Denton, Tr. Vol. VII at 34-35.) As for the effect of Inderal on
Patient No. 2, Dr. Denton testified that he believed the dosage to be
``too small to influence cognitive functioning in any manner.''
(Denton, A-121 at 53.)
The administration of Elavil to Patient No. 2 deserves particular
attention because of the frequency of this drug's administration.
Elavil is a psychoactive drug used in the treatment of depression.
(Zung, Tr. Vol. III at 51.) While the case records in evidence for
Patient No. 2 do not record the administration of Elavil, the testimony
of Dr. Denton, a witness for AHP, indicates that Patient No. 2 received
25 mg of Elavil at night before sleep, but that this medication was
stopped during the last 7 weeks of the study. (Denton, A-121 at 52.)
Since patients were in the Yesavage study for 19 weeks--3 weeks of
prestudy washout followed by 16 weeks in the clinical trial (G-9.2 at
32)--this would mean that Patient No. 2 was receiving Elavil nightly
for the first 12 weeks of the 19 week study.
Despite Patient No. 2's extended use of a psychoactive drug, Dr.
Denton testified that he did not believe that this patient should have
been excluded. (Denton A-121 at 52.) Dr. Denton testified that, while a
``strict interpretation of the protocol might have eliminated'' Patient
No. 2 for the concomitant Elavil use, Dr. Denton nonetheless concluded
that this patient need not be excluded because the administration of
Elavil was stopped during the last two evaluations, ``the crucial ones
from an efficacy standpoint.'' (Denton, A-121 at 52.)
In considering this evidence, the ALJ was not persuaded by Dr.
Denton's explanation for failing to exclude Patient No. 2. The ALJ
found that the question remained as to whether Elavil use during the
beginning of the study could have caused a SCAG score that was worse
than it would have been without the drug. (I.D. at B-1.) When the
Elavil administration was ceased during the final two evaluations, this
alone may have caused any improvement in this Patient's SCAG score.
(I.D. at B-1.) I agree with the ALJ's analysis of this issue, and I
conclude that the concomitant medication use of Elavil by Patient No. 2
was grounds to exclude this patient.
[[Page 64131]]
For the next patient, Patient No. 5, a Cyclospasmol
patient, the case records indicate that this patient received Valium
(diazepam) ``occasionally for nervousness,'' and Inderal ``q.i.d.''
(quater in die, four times a day). (G-12.1 at 212; Denton, A-121 at 51,
53-54.) The case records for this patient do not reveal the dosage for
these drugs, nor is there a contemporaneous medication record tracking
the days or times at which either of these medications were
administered. (See G-12.1 at 206-308.)
Regarding the administration of Inderal, Patient No. 5's case
records do not indicate the dose given, but Dr. Denton testified that
this patient received 10 mg of Inderal four times a day. (Denton, A-121
at 53.) As was previously stated, Dr. Denton also testified that
Inderal in ``a large dose, perhaps more than 80 mg/day, might make
patients confused or depressed.'' (Denton, A-121 at 53.) Other possible
side effects include disorientation, short term memory loss, clouded
sensorium, and decreased performance on neuropsychometric tests.
(Denton, Tr. Vol. VII at 34-35.)
As for the administration of Valium to Patient No. 5, Dr. Denton's
testified as follows:
The hospital records reveal that the Valium was ordered on a prn
(pro re nata, as occasion arises) basis, which suggest that it was
used infrequently, and her referring physician told me by telephone
that it was used 0-2 times per week. There were no medication sheets
on this patient's record.
(Denton, A-121 at 51-52.)
It should be emphasized that Dr. Denton's estimation of the
``infrequency'' of the administration of Valium to Patient No. 5 is
only speculation, in view of the fact that there were no medication
records for Dr. Denton's review, nor is there evidence that this
patient's referring physician based his or her statements on any such
medication records.
I further note that even if Dr. Denton is correct in estimating the
administration of Valium to Patient No. 5 to be as much as 2 times per
week during the 19 week study, that amount of Valium--as much as 38
doses during the study--is a clear violation of the protocol, which
specifies, ``Occasional doses of thioridazine (Mellaril) or diazepam
(Valium) may be used if deemed necessary; however, no more than 16
doses of one of these agents may be taken per study * * * .'' (G-9.2 at
34.)
The absence of detailed records tracking the administration of
Valium and Inderal to Patient No. 5 makes it impossible to fully
evaluate the effect of these concomitant medications. The inadequate
records are a ``fatal flaw'' which can weighed against finding the
Yesavage study to be adequate and well-controlled. (Commissioner's
Decision on OPE, slip op. at 52.)
Patient No. 16, an outpatient and a Cyclospasmol subject,
received 10 mg of Librium, a benzodiazepine, ``only rarely,'' according
to the testimony offered by Dr. Denton. (A-121 at 52.) However, Dr.
Denton gave no specific information regarding the dosage, or dates and
times of administration of Librium, and the records in evidence for
Patient No. 16 contain no information at all pertaining to this
patient's use of Librium. (G-12.4 at 1-100.) The administration of
Librium could have had a confounding effect on the results of this
study, and the absence of medication records is, as with the previous
patient, a ``fatal flaw'' that can be weighed against finding the
Yesavage study adequate and well-controlled. (Commissioner's Decision
on OPE, slip op. at 52.)
Regarding Patient No. 18, a Cyclospasmol subject, Dr.
Denton testified that this patient had been given Sinemet (carbidopa/
levodopa), a drug used in the treatment of Parkinson's disease, between
the ratings taken at weeks 7 and 8. (Denton, A-121 at 50, 54-55.) The
final rating was taken at week nine. (See G-12.4 at 190-201.) Dr.
Denton acknowledged that Sinemet can have a ``positive effect on
cognition.'' (Denton, A-121 at 54; see generally Leber, G-64 at 14
(Sinemet use in Rao study).) Nevertheless, Dr. Denton testified that he
believed that if Sinemet had any effect on Patient No. 18, it was only
to make this patient worse. (Denton, A-121 at 54.) Dr. Denton based his
conclusion on the SCAG scores for Patient No. 18. (Denton, A-121 at
54.) Dr. Denton stated that at baseline this patient's SCAG score was
49, and that at visit 7 the score had improved to 43 (a lower score
being a better score), but that at visit 9 the score was again 49.
(Denton, A-121 at 54.)
I find Dr. Denton's proffered explanation that Sinemet made Patient
No. 18's SCAG score worse to be based on mere speculation. Aside from
the fact that Dr. Denton's explanation was inconsistent with his other
testimony, in which he testified that Sinemet can have a positive
effect on cognition, I note that another possible explanation not
addressed by Dr. Denton is that Patient No. 18's SCAG score might have
deteriorated even further had it not been for the Sinemet.
Additionally, as Dr. Zung, a witness for AHP, testified, there are
instances where patients with Parkinson's disease have a period of
remission or spontaneous improvement with the disease, which could have
a confounding effect on the results of a study. (Zung, Tr. Vol. III at
23.) However, these explanations, too, are speculative.
I note also that, as with the previously discussed Yesavage
patients, the records in evidence pertaining to Patient No. 18 contain
no information regarding this patient's concomitant medications. (G-
12.4 at 101-201.) Once again, I state that the absence of such records
is a fact which can be weighed against finding the study to be adequate
and well-controlled. (Commissioner's Decision on OPE, slip op. at 52.)
Patient No. 24, a Cyclospasmol subject, received both
Inderal and Serax. Dr. Denton testified that this patient received 20
mg of Inderal three times a day, subsequently reduced to 20 mg, twice a
day. (Denton, A-121 at 53.) Dr. Denton did not specify when this change
in dosing schedule was made. However, this patient's clinical records
contain a notation that this patient was on Inderal 20 mg, twice a day,
as of the first visit, which was on January 10, 1982, and the patient
continued this medication throughout the study. (G-12.6 at 12, 28, 41,
56, 59, 62, 71, 78, 87, 94.) As previously discussed, Inderal can cause
side effects such as confusion and depression (Denton, A-121 at 53),
disorientation, short term memory loss, clouded sensorium, and
decreased performance on neuropsychometric tests. (Denton, Tr. Vol. VII
at 34-35.)
As for the administration of Serax, a benzodiazepine, to Patient
No. 24, Dr. Denton testified that 10 mg of Serax was given to Patient
No. 24 at bedtime as a sedative. (Denton, A-121 at 52.) This patient's
clinical records contain no mention of this medication or the frequency
and dosages given. (G-12.6 at 2-104.) This level of administration of a
benzodiazepine certainly violates the intent of the protocol's
concomitant medication restriction, which permits ``(o)ccasional doses
of thioridazine or diazepam,'' but no more than 16 doses per study per
patient, and no more than 3 doses per week. (G-9.2 at 34.) For this
reason, Patient No. 24 should have been excluded. Additionally, the
absence of written records tracking the strength, frequency, and length
of administration of this drug can be weighed against finding the
Yesavage study to be adequate and well-controlled. (OPE, slip op. at
52-53.)
Patient No. 34 and Patient No. 37 both had Parkinson's disease. (G-
12.7 at 210 (Patient No. 34); G-12.8 at 109, 113 (Patient No. 37);
Mohs, G-62 at 16; Thal, G-63 at 12.) Patient No. 34, a
Cyclospasmol subject, received 25 mg of Benadryl twice a day.
(G-12.7 at 217; Mohs, G-62 at 16; Thal, G-63 at 12.)
[[Page 64132]]
Benadryl is a drug which has indications for use for patients with
Parkinson's disease. (Zung, Tr. Vol. III at 52; see also G-12.7 at
217.) The side effects of Benadryl can include diminished mental
alertness, sedation, sleepiness, dizziness, and confusion. (Zung, Tr.
Vol. III at 52.) Phenergan, an antiemetic, was also given to this
patient. (Denton, A-121 at 52.)
Patient No. 37, also a Cyclospasmol subject, received
Sinemet 25/100 (25 mg carbidopa/100 mg levodopa) every four hours to
control symptoms of Parkinson's disease. (Mohs, G-62 at 16; Thal, G-63
at 12; Denton, A-121 at 54.) This patient also received 25 mg of Elavil
twice a day. (G-12.8 at 114.) The frequency of administration of
Elavil, a psychoactive drug (Zung, Tr. Vol. III at 51), warranted the
exclusion of Patient No. 37.
Additionally, as I ruled in a previous discussion, both Patient 34
and Patient 37 should have been excluded because of their concomitant
Parkinson's disease. (See section I.D.2.a. of this document.) Moreover,
I rule that the concomitant medication use by these patients can be
weighed against finding the Yesavage study to be adequate and well-
controlled because the effect of the concomitant drugs may have
confounded the results now attributed to Cyclospasmol.
Patient No. 7, a placebo patient, received Inderal twice a day
during the study. (G-12.2 at 7.) The case records for this patient do
not record the dose for this drug. However, Dr. Denton testified that
Patient No. 7 received 10 mg of Inderal twice a day. (Denton, A-121 at
53.) Inderal can affect cognition. While this level of Inderal use may
not itself be reason to exclude this patient, nevertheless, the
possible confounding effect of this drug's side effects can be taken
into consideration. Additionally, the failure of the case records to
document Patient No. 7's concomitant medication use can be considered
in evaluating the Yesavage study. (Commissioner's Decision on OPE, slip
op. at 52-53.)
Regarding Patient No. 9, a placebo patient, Dr. Denton testified
that orders were given for this patient to receive 15 mg of Dalmane at
bedtime ``PRN.'' Dr. Denton conceded that Dalmane, a benzodiazepine,
``might be considered a contraindicated medication.'' (Denton, A-121 at
56.) However, Dr. Denton testified that Patient No. 9 was only given
Dalmane once during the study--on September 14, 1981--and for this
reason Dr. Denton did not believe this medication confounded the study.
(Denton, A-121 at 56.) The final evaluation of this patient occurred on
September 17, 1981.
The clinical documents in evidence contain no record of Patient No.
9 being administered Dalmane. (G-12.2 at 104-205.) A single
administration of a benzodiazepine would not appear to be confounding
to this study. Nonetheless, the actual administration of Dalmane is not
corroborated in this patient's case records. The failure of the case
records to document the actual administration of Dalmane can be weighed
against finding the Yesavage study to be adequate and well-controlled.
(OPE, slip op. at 52-53.)
Patient No. 21, also a placebo patient, received 25 mg of Mellaril
(thioridazine hydrochloride) twice a day throughout the study. (Denton,
A-121 at 55-56.) This patient's clinical records now in evidence
contain no record of Patient No. 21 having received Mellaril. (G-12.5
at 105-208.) Mellaril can affect cognitive performance and cause a
patient to perform worse on cognitive tests than he or she might have
but for the Mellaril. (Leber, Tr. Vol. I at 69.) Administration of
Mellaril at this frequency was clearly a violation of the protocol,
which restricted thioridazine to occasional doses. (G-9.2 at 34.) This
patient should have been excluded.
Regarding Patient No. 33, the Center had argued that this patient
should have been excluded on the basis that this patient received the
concomitant medication of Elavil during the study. (Center Post-Hearing
Brief at 81 & Attachment D.) This patient's records do not reveal
whether this patient was a placebo patient or a Cyclospasmol
patient, and Patient No. 33's medication use was not discussed by Dr.
Denton in his testimony.
Regarding Patient No. 33's concomitant medication use, a notation
in this patient's records of the prestudy evaluation indicates that
this patient had received 25 mg of Elavil twice a day from January 4,
1979, through May 18, 1982. There are no medication records in evidence
but, based upon this notation in the prestudy evaluation, it appears
that the administration of Elavil was reported to have been stopped 2
weeks before Patient No. 33 was accepted into the Yesavage study. (G-
12.7 at 112.)
Other patient records in evidence indicate that this patient's
first visit during the study occurred on August 2, 1982. (G-12.7 at
128.) According to the protocol, at the first visit the patient was to
enter into a single-blind washout period. (G-9.2 at 36, 38.) This
washout period was to last until the patient's second visit, at which
point the patient entered the double-blind medication phase of the
study. (G-9.2 at 168.) A further notation in this patient's records
from this patient's second evaluation, which occurred on August 24,
1982, states, ``Elavil still discontinued for length of study.'' (G-
12.7 at 143.)
Although daily medication records are not in evidence for Patient
No. 33, I nevertheless rule, based upon the records which are in
evidence, that Patient No. 33 properly was included in the study. Based
upon the evidence, it does not appear that this patient was receiving
the concomitant medication of Elavil during the study.
Patient No. 35, a placebo patient, received Haldol during the
study. (Denton, A-121 at 56.) This patient's clinical documents in
evidence contain no record of this patient's receiving this medication.
(G-12.8 at 104-205.) Nonetheless, Dr. Denton testified that Patient No.
35 received a single, 1 mg dose of Haldol, 9\1/2\ weeks before final
evaluation. (Denton, A-121 at 56.) However, Dr. Denton's testimony
appears inconsistent on this point, because he also testified that
Patient No. 35 received Haldol ``b.i.d.,'' that is, bis in die, or
twice a day.
Additionally, I note that Patient No. 35's clinical records
indicate that this patient received 10 mg of Isordil, a vasodilator,
four times a day throughout the study. (G-12.8 at 11, 40, 56, 59, 62,
71, 78, 87, 94.) This could have caused a confounding effect. Neither
the Center nor AHP address this part of the patient's record, nor does
the ALJ discuss the apparent concomitant Isordil use. Although there is
sufficient evidence for me to conclude that Isordil was administered
concomitantly, I will, in view of the fact that no party addressed this
issue, instead weigh this evidence as a deficiency in the clinical
records for the Yesavage study. (Commissioner's Decision on OPE, slip
op. at 52-53.)
To summarize, a pervasive problem with the Yesavage study is the
failure to adequately document concomitant medication use. In many
instances, the case records do not even mention the concomitant
medication at issue. In other instances, the medication is listed but
the dosage is not, nor is the schedule of administration for the drug.
The use of concomitant medications is an important matter.
Uncontrolled use of concomitant medications defeats the scientific
value of a study. (Commissioner's Decision on OPE, slip op. at 204.)
Vague or incomplete records of concomitant medications are ``fatal
flaws'' which weigh heavily against finding a study adequate and well-
controlled. (Id. at 53.) Also, the number of various concomitant
medications
[[Page 64133]]
increases the difficulty of evaluating Cyclospasmol's effect.
(Id. at 56.) Additionally, the proportionately large number of patients
receiving concomitant medications--12 out of 23 patients in the final
analysis--weighs against finding the Yesavage study adequate and well-
controlled. (Id. at 57.)
I conclude by ruling that, based upon both the patient case records
and testimonial evidence, Patient Nos. 2, 24, 37, and 21 should have
been excluded for concomitant medication use. Regarding Patient Nos. 5,
16, and 35, their concomitant medication use could not be properly
evaluated because of incomplete case records. The testimony offered by
Dr. Denton regarding Patient Nos. 5, 16, and 35 was vague and was not
sufficient to evaluate these subjects. This absence of documentation of
concomitant medication use can be weighed against finding the Yesavage
study to be adequate and well-controlled.
As for Patient Nos. 7 and 9, assuming for the purposes of this
discussion that Dr. Denton's testimony completely and accurately
described these patients' concomitant medication use, then these two
patients were possibly properly included. However, the medication
regimens for Patient Nos. 7 and 9 were not corroborated in their case
records, which weighs against finding the Yesavage study to be adequate
and well-controlled.
Regarding Patient Nos. 34 and 37, I previously ruled that these
patients should have been excluded for Parkinson's disease. I note that
I have additionally found that Patient No. 37 should have been excluded
for concomitant medication use.
As for Patient No. 18, if concomitant medication use alone is
considered, and, assuming that Dr. Denton's testimony completely and
accurately describes this patient's concomitant medication use, then
this patient may properly have been included. However, the failure of
the case records to document this patient's concomitant medication use
weighs against finding the Yesavage study to be adequate and well-
controlled. Furthermore, I previously found that Patient No. 18's case
records seem to indicate that this patient had Parkinson's disease.
AHP's failure to address this patient's apparent concurrent Parkinson's
disease can be weighed against finding the Yesavage study to be
adequate and well-controlled.
Regarding Patient No. 33, it appears from the records in evidence
that this patient was not receiving the concomitant medication of
Elavil during the study.
Overall, I find that the uncontrolled use of concomitant medication
and the poor documentation of concomitant medication use weighs against
finding the Yesavage study to be adequate and well-controlled.
e. Small sample size. AHP argues that the ALJ erred in ruling that
in view of the small sample size in the Yesavage study--12
Cyclospasmol patients and 8 placebo patients at week 16--it
was ``inappropriate to generalize the results.'' (AHP Exceptions at
166, quoting I.D. at 57.) On this point, the ALJ also had noted that
earlier in the study, at week 12 when 14 Cyclospasmol
patients and 9 placebo patients were tested, there was no statistically
significant drug effect. (I.D. at 52.) However, at week 16, when three
patients had been dropped from the study, statistical significance was
reported. (I.D. at 52, citing Thal, G-63 at 17.) While the ALJ found
that there had been no showing that the dropping of the three patients
resulted in statistical significance, the ALJ nevertheless observed,
``The problem with such a small sample size is that the omission of one
or two patients can change the results rather dramatically.'' (I.D. at
52.) AHP objects to the ALJ's opinion on these points.
In support of its argument, AHP cites the testimony of Dr. Mantel,
a statistician and witness for AHP, who, in connection with his
testimony pertaining to the MDS-96 study, testified as follows
regarding small studies:
As to Dr. Reich's comment that ``most often a larger sample
provides more convincing conclusions than a small one,'' Dr. Reich
is correct. If I wished to have my study provide more convincing
conclusions, I would conduct a larger study employing a larger
sample. But once a study is completed that argument is no longer
relevant. A significant result from a small study is, nevertheless,
a significant result. And a significant result from a small study
would betoken an important effect. Large studies would very likely
yield statistical significance if the true effect were important.
But with a very large study even a minor treatment effect would lead
to a statistically significant outcome. It is recognized that the
hypothesis of absolutely no treatment effect is almost never exactly
true--thus, statistical significance could reflect large study size
yet only a very minor treatment effect. * * * As indicated above,
statistical significance despite limited study size would betoken an
important treatment effect.
(Mantel, A-127 at 7-8.)
AHP also cites the testimony of two other of its witnesses, Mr.
Danny S. Chaing and Dr. John E. Overall, who testified regarding
statistical power and sample size in the Yesavage study. On this
matter, Mr. Chaing testified, ``(The) Yesavage sample is large enough
to produce reliable and generalizable conclusions * * *. (T)here's no
single minimum required sample size.'' (Chaing, Tr. Vol. I at 22-23.)
Dr. Overall testified, ``There's no merit in the criticism that a
sample is too small from an appropriately designed and conducted study
which has produced statistically significant results.'' (Overall, Tr.
Vol. II at 55.)
AHP further argues that if a small study yields a result that is
statistically significant, this suggests that the drug effect is
``large'' because ``the variability of human response would make it
unlikely that statistical significance would be achieved in a small
study if the drug effect were small.'' (AHP Exceptions at 167.) The
Center counters that AHP is confusing the size of the drug effect with
the variability inherent in a small sample. (Center Response to AHP
Exceptions at 69.) The Center further argues that in a small study,
regardless of the size of the drug effect, the results from only one or
two subjects can completely alter the study's results. (Center Response
to AHP Exceptions at 69.) I find the Center's arguments to have merit.
Small samples have larger standard errors, i.e., the uncertainty in
the results encompasses a greater range of values by which the mean of
the population may vary. The size of the standard error from a study is
a measure of the degree to which the study's results reflect the true
value which would have been found in the population-at-large having the
disease or condition. In studies based on small samples, results may
differ greatly from one study to the next because the results of only a
few subjects can greatly affect the outcome of the study.
While a small sample study can indicate a statistically significant
result, I note that the problem with a small sample is that its larger
standard error can make it difficult to identify, with a useful degree
of precision, the true value or result which would be found in the
larger population having the disease or condition under study. This
concern was expressed in the testimony of Dr. Thal, a witness for the
Center, who testified, ``(A)s the number of patients in a study
decreases, the chance variation or the variability introduced by a
single one or two patients grows.'' (Thal, Tr. Vol. VI at 48-49.)
Because of the larger standard error with a small sample, the
results from a study conducted on a small sample may not reflect the
true value which would have been obtained from the population-at-large
having the disease
[[Page 64134]]
or condition under study. Evidence of effectiveness can be drawn from
small samples, but for the evidence to be reliable the sample needs to
be carefully selected beforehand. The sample must be representative of
the larger population having the disease or condition under study.
The problems of generalizing results from a small study were also
at issue in the Commissioner's Decision on OPE, which stated:
(A) statistically significant result, when based on a sample
size of only five subjects, does introduce the strong likelihood
that the subjects were not representative of the larger population
from which the sample was drawn, and that there may be an
inadvertent lack of comparability in the test and control groups,
contrary to the requirements of (the regulations).
(Commissioner's Decision on OPE, slip op. at 117; cf. Commissioner's
Decision on Lutrexin, 41 FR 14406 at 14419 (In a study with a total of
32 patients, the small size of the sample was identified as a factor
which ``aggravated'' the problems arising from the unreliability of the
diagnostic criteria used in the study.))
For the above discussed reasons, I therefore find that the ALJ was
correct in observing that the omission of one or two patients can
change the results of a small sample study (I.D. at 52), and was
correct in questioning whether it was appropriate to generalize the
results of the Yesavage study. (I.D. at 57.)
As for AHP's argument that a statistically significant result in a
small sample indicates that the drug effect is ``large,'' I find this
statement to be inaccurate and misleading. (See AHP Exceptions at 167,
citing Mantel, A-127 at 7-8.) AHP seems to be implying that a
statistically significant result in a small study necessarily means
that the test drug had a significant clinical effect. This implication
is incorrect.
Statistical significance is not the same as clinical significance.
(Commissioner's Decision on Benylin, 44 FR 51512 at 51521.) Statistical
significance is an expression of the probability that an observed
difference between the mean outcome of the test drug group and the mean
outcome of the control drug group occurred by chance. (Commissioner's
Decision on Benylin, 44 FR 51512 at 51520.) A clinically significant
effect, however, is an expression of the degree of benefit which was
observed in the study's patients and which may be expected in future
patients. (Commissioner's Decision on Benylin, 44 FR 51512 at 51520.)
As has been noted in previous Commissioner's decisions, it is
possible to achieve a statistically significant difference between
treatment and control groups in a clinical trial, yet the test drug may
be found not to have had a clinically significant effect, i.e., the
effect on the patient is not beneficial either in degree or type of
effect. (Commissioner's Decision on Lutrexin, 41 FR 14406 at 14419;
Commissioner's Decision on Benylin, 44 FR 51512 at 51520 and 51521;
Commissioner's Decision on Mysteclin, slip op. at 24-29.) Estimates of
clinical significance take into consideration other matters beyond a
finding of statistical significance, such as identifying which
parameters were said to have shown statistical significance and
deciding whether those parameters are important in a clinical setting.
These considerations are further discussed in the next section of this
decision. (See section I.D.2.f. of this document.)
Therefore, for the foregoing reasons, I find that the ALJ was
correct in considering the small sample size as a factor to be
considered in reviewing the results of the Yesavage study.
f. Clinical significance. AHP next argues that the ALJ erred in
finding that the improvement on SCAG Factor 1 was not clinically
significant. (AHP Exceptions at 169, citing I.D. at 54, 57.) As was
previously described (see section I.D.2.c. of this document), SCAG
Factor 1, ``cognitive dysfunction,'' included the following four items:
(1) Confusion, (2) impaired mental alertness, (3) impaired recent
memory, and (4) disorientation. (G-11.1 at 70.) AHP argues that the
outcome on SCAG Factor 1 was clinically significant because dementia is
a progressive disease, and that any small improvement would be
important to both the patient and the physician. (AHP Exceptions at
170.)
The ALJ's finding was based on the testimony of two witnesses for
the Center, Drs. Mohs and Thal. These witnesses both testified that the
absolute magnitude of change from baseline for SCAG Factor 1 was very
small, approximately 1.9 change on a scale on which patients in the
study had been shown to have a baseline value of 14.1. (Mohs, G-62 at
18; Thal, G-63 at 15-16.) Drs. Mohs and Thal testified that this degree
of change--a 14 percent improvement on one SCAG Factor--would not be
evident to most observers. (Mohs, G-62 at 18; Thal, G-63 at 15-16.) It
should be noted that the lowest/best score on SCAG Factor 1 would be a
4; the highest/worst score would be a 28. (See, e.g., G-12.1 at 38.)
This would mean that from a baseline score of 14.1, the score on SCAG
Factor 1 had lowered/improved to approximately 12.2.
On the other hand, three witnesses for AHP--Drs. Overall, Zung and
Klerman--testified that because dementia has no known cure and because
this disease is a progressive one, a 14 percent improvement on one SCAG
factor is, in their opinions, clinically significant. (Overall, Tr.
Vol. II at 49; Zung, Tr. Vol. III at 7; Klerman, Tr. Vol. III at 70-
71.) Based on the testimony of these witnesses, AHP essentially is
arguing that any statistically significant result on any one of the
several tests used in the Yesavage study is necessarily clinically
significant because there is no known cure for dementia. I do not find
this argument to be persuasive.
In the United States Supreme Court decision of United States v.
Rutherford, 442 U.S. 544 (1979), the Court recognized that the
statutory requirement of proof of effectiveness necessarily required a
showing of some clinical benefit to the patient. In relevant part, the
Court stated, ``(I)n the treatment of any illness, terminal or
otherwise, a drug is effective if it fulfills, by objective indices,
its sponsor's claim of prolonged life, improved physical condition, or
reduced pain.'' (442 U.S. at 555.) Consistent with the Rutherford
decision, the United States Court of Appeals for the Third Circuit has
ruled that it is within the purview of the FDA to decide whether a drug
has clinical significance. (Warner-Lambert, 787 F.2d at 154-56; see
also Commissioner's Decision on Mysteclin, slip op. at 24.)
To reiterate some of the discussion of the previous section (see
section I.D.2.e. of this document) regarding the difference between
statistical and clinical significance, a drug can have a statistically
significant effect without having a clinically significant effect.
Statistical significance is an expression of the probability that an
observed difference between the test drug and the control drug occurred
by chance. Clinical significance, on the other hand, is an evaluation
of whether the test drug offers a therapeutic benefit to the patient.
(Commissioner's Decision on Mysteclin, slip op. at 25; Commissioner's
Decision on Benylin, 44 FR 51512 at 51520 and 51521; Commissioner's
Decision on Lutrexin, 41 FR 14406 at 14419.) Proof of statistical
significance is insufficient without proof of clinical significance.
(Commissioner's Decision on OPE, slip op. at 60-62.) As the Court in
Warner-Lambert noted:
The fact that the drug, not chance, can be assumed to have
contributed to (the finding of statistical significance for) the
factor measured does not necessarily establish that patients will
receive a benefit from the drug.
[[Page 64135]]
The Commissioner has consistently required a showing of some benefit
as an element of the statutory requirement of effectiveness.
(Warner-Lambert, 787 F.2d at 155 (citation omitted).)
Turning now back to the evidence at hand, AHP's argument in favor
of finding clinical effectiveness for Cyclospasmol was
expressed in the testimony of Dr. Zung, an AHP witness, who testified
as follows:
I would say that first of all, we are dealing with an illness,
which is the dementias, where we know that there has been no drug
available for the treatment of this disease so that there has been
no improvement whatsoever on any drug that's known. So here we're
talking about an illness with progressive deterioration so,
therefore, in fact any treatment that would either arrest the
development of the illness or in fact improve the illness would
definitely be significant. Factor 1 of the SCAG then, in fact, is
specific to measure the cognitive dysfunction that's associated with
the dementia and that, of course, has been the indication for which
the drug has been studied.
(Zung, Tr. Vol. III at 7-8.)
In contradistinction to Dr. Zung's testimony, the testimony offered
by Dr. Mohs, a witness for the Center, was as follows:
The absolute magnitude of change was very small for the
cognitive factor in the SCAG, approximately 1.9 on a scale that had
a baseline value of 14.1. This change would not be evident to most
observers. Also, there was no corroboration even as a trend on the
other measures, such as, the NOSIE, the Buschke memory test or the
clinical global evaluation. Finally, there is a discrepancy between
the overall item, item 19 on the SCAG, and (the) clinical global
item completed by the investigator at the end of the study. The
overall item on the SCAG did tend to show an improvement for the
Cyclospasmol group, whereas the clinical global item
completed at the end of the study did not show any significant
effect and these items presumably should be highly cor(r)elated.
Because the effect claimed is so small, not corroborated by other
tests, and in fact inconsistent with tests that measure the same
effect, I do not find the results to be clinically significant.
(Mohs, G-62 at 18.)
Similar testimony was offered by Dr. Thal, another witness for the
Center, who testified with reference to Cyclospasmol, ``If
the drug fails to show a clinically significant improvement on any
global or clinical evaluation scale and fails to make a meaningful
difference in the way a (patient) lives his or her life, one must
seriously question whether that drug should be marketed for a specific
indication.'' (Thal, G-63 at 16.)
Having reviewed the evidence, I do not find AHP's argument to be
persuasive. There is no indication that the results on SCAG Factor 1
will translate into a clinically meaningful reversal or slowing of the
progress of dementia. Moreover, AHP's witnesses failed to address the
fact that the statistically significant result on SCAG Factor 1 stands
alone and is not corroborated by the other measures.
I further note that when a comparable argument was advanced by the
manufacturer in the Commissioner's Decision on Lutrexin, that decision
ruled that, notwithstanding the fact that there may be no alternatives
for the proposed indication for the drug under review, the act
nonetheless requires that the effectiveness of a drug be demonstrated
by substantial evidence. The Commissioner's Decision went on to note
that this requirement does not result in depriving patients of the only
known effective drug therapy for a proposed indication because, absent
scientifically reliable evidence, that particular drug is not proven to
be effective for that indication. (Commissioner's Decision on Lutrexin,
41 FR 14406 at 14411.)
For these reasons, I do not find that AHP has fulfilled the
requirement of proving clinical significance.
g. Multiple tests. In the Yesavage study, 28 outcome measures were
statistically analyzed, including the Nurses Observation Scale--
Inpatient Evaluation (NOSIE) score, the Hamilton Depression Scale, the
BMT, the clinical global impression score, and the 24 measures--5
factors plus 19 items--on the Sandoz Clinical Assessment--Geriatric
(SCAG) measure. (G-9.2 at 45.) Each of these measures was also assessed
for six time periods during the study, including at baseline and at
weeks 3, 6, 9, 12, and 16. (G-11.1 at 29-37.) Of these 28 outcome
measures, 2 measures--SCAG Factor 1 (``cognitive dysfunction'') and
SCAG Item 19 (``overall impression of patient functional capacity'')--
showed statistical significance in favor of the Cyclospasmol
group, based upon the results of the 20 patients whose outcomes were
included in the final analysis of the SCAG. (G-11.1 at 19-20, 29, 78;
Thal, G-63 at 16-17; Chaing, Tr. Vol. I at 52-53; Overall, A-116 at 6.)
AHP argues that the results of SCAG Factor 1 are ``the most
relevant and important indicator'' of the efficacy of
Cyclospasmol for senile dementia.7 (AHP Post-Hearing
Brief at 116.) However, the ALJ ruled that because the number of tests
and outcome measures for each patient in the Yesavage study were so
numerous, it was ``difficult to draw definitive conclusions from the
fact that statistical significance was found on one factor (SCAG Factor
1).'' (AHP Exceptions at 172, quoting I.D. at 54.) AHP argues that this
was error, and AHP further argues that the fact that multiple outcome
measures were used does not lessen the strength of its SCAG Factor 1
finding, nor the SCAG Item 19 finding, which was also reported to have
been statistically significant. (AHP Post-Hearing Brief at 117.) AHP
additionally argues that because the various outcome measures were
specified in the protocol, the multiple statistical analyses were not
performed to generate a post hoc hypothesis. (AHP Post-Hearing Brief at
116.)
---------------------------------------------------------------------------
\7\ I note that there was a difference between SCAG Factor 1 in
the Yesavage study, and SCAG Factor 1 in the Rao study. In the
Yesavage study, SCAG Factor 1 was called ``Cognitive Dysfunction,''
and it was comprised of SCAG Items 1 through 4. In the Rao study,
SCAG Factor 1 was called ``Mental Dysfunction,'' and it was
comprised of SCAG Items 1 through 4 and Item 8. (Chaing, Tr. Vol. I
at 47.)
---------------------------------------------------------------------------
The Center argues that the ALJ was correct in his ruling, and also
argues that the statistically significant results on SCAG Factor 1 and
SCAG Item 19 may be due to the multiple statistical tests employed.
(Center Post-Hearing Brief at 90-92; see also Mohs, G-62 at 17; Thal G-
63 at 16.) The Center argues that cognitive dysfunction is only one
aspect of senile dementia, and that senile dementia has many
manifestations besides that of cognitive impairment, such as
impairments in social functioning, orientation, personality, and the
ability to speak (aphasia). (Center Post-Hearing Brief at 91, citing
Zung, Tr. Vol. III at 43-44.) The Center points to the fact that AHP
did not specify cognitive impairment, either on SCAG Factor 1 or SCAG
Item 19, as the parameter of interest in advance of the study. (Center
Response to AHP Exceptions at 73.) In support of its argument, the
Center quotes from the Yesavage study's protocol as stating more
generally that the purpose of the study was to evaluate
Cyclospasmol ``in improving symptoms usually associated with
brain function.'' (Center Post-Hearing Brief at 90-91, quoting G- 9.2
at 32.)
The Center also cites to the testimony of Dr. Zung, a witness for
AHP. (Center Response to AHP Exceptions at 72-73.) When Dr. Zung was
asked how corrections for multiple comparisons are performed, he
replied that there are two methods for making such corrections. The
first is to specify in advance, before the statistical analysis is
performed, the parameter of interest. The second method is to employ a
statistical correction for the number of multiple comparisons which
were made. (Zung, Tr. Vol. III at 62-63.) The Center argues that such
corrections should have been
[[Page 64136]]
made in the Yesavage study. I find the Center's arguments to have
merit.
A comparable issue was adjudicated in the Commissioner's Decision
on Mysteclin. Therein, it was ruled, ``(E)ven if the subgroups and
multiple endpoints had been identified in the protocol, * * * some
downward adjustments in the p values should have been made to correct
for the analyses of multiple subgroups and endpoints.'' (Commissioner's
Decision on Mysteclin, slip op. at 43; see also Commissioner's Decision
on Deprol, 58 FR 50929 at 50933.) Similarly, in the Commissioner's
Decision on Deprol, it was noted that, ``if enough pair-wise
comparisons are made, some comparisons will be `statistically
significant' by chance alone.'' (Commissioner's Decision on Deprol, 58
FR 50929 at 50933.) When multiple comparisons are made, corrections in
the p values are needed to maintain the correct Type I error rate
because the likelihood of a Type I error increases with the number of
individual comparisons. (Commissioner's Decision on Deprol, 58 FR 50929
at 50933.) In other words, as one great author more expressively
observed, ``Fortune brings in some boats that are not steered.''
(Shakespeare, Cymbeline, IV, iii, 46.)
For these reasons, I find that in weighing the adequacy of the
Yesavage study, it is proper to consider the fact that numerous
statistical analyses were employed, and to consider that the particular
outcome of interest was not specified in advance, nor were adjustments
to the p value made. Accordingly, I find no error in the ALJ's ruling
on this point.
h. Adequacy of the Yesavage study. In sum, I find that the Yesavage
study was not adequate and well-controlled. In making this
determination, I have considered the aggregate effect of the protocol
violations. I base my ruling upon these findings: (1) That the
selection of patients for the study was flawed by the inclusion of
patients with the concomitant condition of Parkinson's disease, and by
the inclusion of outpatients, who were to be excluded under the
protocol; (2) that the failure to show that stroke patients were
included in both the drug and the placebo arms of the clinical trial
can be considered as a flaw in the study; (3) that the fact that a
statistically significant difference between test and control groups
existed on the BMT was a proper consideration; (4) that the
uncontrolled use of concomitant medication and the poor documentation
of concomitant medication use weighs against finding the Yesavage study
to be adequate and well-controlled; (5) that the small sample size was
a proper factor to be considered in reviewing the results of the study,
and can be weighed against the adequacy of the study; (6) that the
improvement of patients on SCAG Factor 1 was not clinically
significant; and (7) that the fact that numerous statistical analyses
were employed and that the particular outcome of interest was not
specified in advance, nor were adjustments to the p value made, can be
weighed against the adequacy of the study.
II. Conclusion and Order
The foregoing opinion in its entirety constitutes my findings of
fact and conclusions of law. Based on the foregoing discussion,
findings, and conclusions, I affirm the ALJ's Initial Decision in all
respects, except where specifically stated otherwise. I find that there
is a lack of substantial evidence that Cyclospasmol will have
the effect it purports or is represented to have under the conditions
of use prescribed, recommended, or suggested in its labeling.
Accordingly, under 21 U.S.C. 355(e)(3), the NDA for
Cyclospasmol must be withdrawn. I further find that, by
reason of the lack of substantial evidence of its effectiveness,
Cyclospasmol is a ``new drug'' within the meaning of 21
U.S.C. 321(p).
Therefore, under the Federal Food, Drug, and Cosmetic Act, 21
U.S.C. 355(e), and under authority delegated to me by the Secretary
(Sec. 5.10(a)(1)), the new drug application for Cyclospasmol
and all amendments and supplements thereto, are hereby withdrawn,
effective January 2, 1997.
Dated: November 12, 1996.
Michael A. Friedman,
Deputy Commissioner for Operations.
[FR Doc. 96-30648 Filed 12-2-96; 8:45 am]
BILLING CODE 4160-01-P
