Suppl. XIX, 66, 66,Suppi. ncer (1992), (1992), XIX, S35 537 Br. J. Cancer
S35-S37
©
Ltd., (D Press Ltd., Macmillan Macmillan Press
1992
1992~~~
Antiemetic study design: A discussion of Dr Olver's paper S. Groshen Department of Preventative Medicine, University of Southern California School of Medicine, Los Angeles, California, USA.
I would like to start by complimenting Dr Olver on a lucid and comprehensive paper. Since I quite agree with his comments, I will take the opportunity to expand on some of the issues he has briefly mentioned. The design of any clinical trial, not just an antiementic trial, should be largely determined by the goals and methods of the analysis, which in turn reflect the objectives of this study. Thus, I will begin by mentioning issues regarding the data analysis.
Role for multivariate analyses As Dr Olver and others have mentioned, the choice of measures of efficacy is one of the more challenging aspects of designing an antiemetic trial. Since we are concerned with several measures of efficacy in antiemetic trials (e.g. nausea, vomiting, and toxicity), we would benefit from examining these outcome measures jointly. Take as an example, the simple trial in which we have studied one antiemetic drug with two measures of efficacy, the number of episodes of vomiting within the first 24 h of chemotherapy administration and the number of hours that the patient felt nauseated during the same 24 h period. For purposes of this illustration, we will ignore side effects and assume that the patients and their chemotherapy are all relatively homogeneous. Suppose the results-univariately-are as given in Figures la and b. There are 40 patients; 50% have no emetic episodes and 30% experience no nausea. In Figures 2a and b two possible patterns of nausea and vomiting for the same 40 patients are plotted. We would draw different conclusions regarding the efficacy of this antiemetic drug, depending on whether the relationship between number of episodes and time nauseated resembled Figure 2a or Figure 2b. In the first example, 12 of the 40 patients experienced no emetic episodes and no nausea; an additional eight experienced only one-half hour of nausea. We might conclude that with this chemotherapy/antiemetic combination, 20/40 or 12/40 of the patients experience no or negligible nausea and no vomiting. On the other hand, in Figure 2b, all of the patients with no vomiting experienced at least one hour of nausea. Thus 100% of patients experienced some side effects to chemotherapy. This type of approachmultivariate analysis -will be necessary for understanding the overall effect of antiemetic agents.
Eligibility and evaluability criteria and analysis on an intent to treat basis Inclusion and exclusion criteria involve information which is available to the study co-ordinators BEFORE a patient is registered into the trial and (if appropriate) randomised. As Dr Olver has mentioned, these criteria should be objective, amenable to documentation, and unambiguous. All registered patients (registered for study participation, not to be confused with the separate registration which often takes place for screening) must be included and accounted for in the final analysis. The screening and registration process must be taken very seriously; this is the time during the trial when investigators have complete control. Once a patient is registered and treatment has started, the patient is usually classified as evaluable or not. The labels 'evaluable' or 'inevaluable' are based on information obtained after registration, assignment of treatment and usually, after start of treatment. A patient can be inevaluable
for two reasons: the measures of efficacy were not obtained or the patient was not 'adequately treated'. There is no satisfactory way to deal with patients missing their measurements of efficacy. We should assess the impact of these patients on the conclusions: include them as failures, include them as successes, and exclude them. If the results are consistent-that is, if the conclusions do not change-then we must report this and use the more conservative version of the analysis. If the conclusions are inconsistent, then this must be reported and a decision made as to whether or not the study should be repeated. If the treatment was inadequate or not done according to protocol, then this patient must be included in the results (with enough information given to allow the reader to evaluate the impact of excluding the subject). Thus, even though a study participant has been labelled 'inevaluable', outcome information must be measured and recorded for analysis. In a randomised study, we must analyse the results on an 'intent to treat' basis. If there are compelling reasons, we may decide to look at the data with the 'inevaluable' patients deleted and compare the conclusions. But our reference is always the 'intent to treat' analysis-i.e. we include ALL patients randomised and classify them according to the randomisation outcome. There are no easy solutions for dealing with inevaluable patients-the best strategy is to avoid the problem and, failing that, to document what has been done. A large number of inevaluable patients will compromise the impact and conclusions of any trial.
a (A
+.O CL a) o
0L
.0
E z
Number of emetic episodes
U)
a)
0.
0)
a) 0
0) E
CO
I0I
z
Number of hours of nausea Figure 1 a Distribution of patients according to the number of emetic episodes experienced during the 24 h after chemotherapy (total of 40 patients). b Distribution of patients according to the duration (in hours) of nausea during the 24 h after chemotherapy (total of 40 patients).
S. GROSHEN
S36
a
.
87en
um
100 PATIENTS
Course 2
CONTINUE TREATMENT 60 PATIENTS
Course 3
CONTINUE TREATMENT 36 PATIENTS
Course 4
CONTINUE TREATMENT 22 PATIENTS
a
MAJOR RESPONSE
:
6543-
Course 1
MAJOR
3+
3+
I
MAJOR
:u:::
o
-1-
-
TTT
-1
0
6 7 8 Number of emetic episodes 2
1
0
3
4
5
9
10
CA
b
0
A 00 ~~~ ~~~~~~ ~~~~~~~~~~~~ ~~~ ~~~
~~~
~~~
U,
76-
C3 5-
I
I*I-
43-
21I
-1V
II
-1
0
II
I
I
1
2
3
4
EMETIC EPISODES OFF-STUDY 14 PATIENTS
I
I
I
I
I
5
6
7
8
9
MAJOR RESPONSE
13 PATIENTS
3+
EMETIC EPISODES 9 PATIENTS
Figure 3 Evaluation of an anti-emetic agent over four courses of chemotherapy and the number of patients treated at each course. Major response = 0-2 emetic episodes during the 24 h after chemotherapy.
~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~
8a)
EMETIC EPISODES OFF-STUDY 24 PATIENTS
I
I
-1
3+
EMETIC EPISODES OFF-STUDY 40 PATIENTS
I
10
Number of emetic episodes Figure 2 a Distribution of patients (total 40) where the number of emetic episodes and duration of nausea (in hours) are positively correlated. b Distribution of patients (total 40) where the number of emetic episodes and duration of nausea (in hours) are inversely correlated.
Denominator in trials with multiple courses When we evaluate the antiemetic efficacy of a drug over several courses, the temptation is to include only those patients who begin each course in the analysis of subsequent courses. This can lead to very different and potentially misleading statements. Consider the example in Figure 3 where only subjects with a major response (0, 1 or 2 emetic episodes during the first 24 h) are given the same antiemetic agent in the next course of chemotherapy. Suppose that with this drug, 60% of subjects, who had a prior major response, have a major response at the current course-always. The expected results are: (1) at each course 60% of patients who NEVER had three or more emetic episodes, had a major response and (2) by the end of the fourth course, only 13% of patients were ALWAYS responders. Because the criteria for selecting and treating patients, on subsequent courses are usually different from the criteria for selecting them for the first course, care must be taken to describe the initial denominator (the number of patients who were treated at the first course) as well as the number of patients treated at each of the later courses. The denominator should be the number of patients, and not the number of courses.
Selection ofpatients for antiemetic studies Once doses and schedules have been chosen for a particular antiemetic drug or set of agents, based on animal studies and Phase I trials, trials to assess efficacy are planned. These efficacy trials fall, broadly, into two types. The first group includes those trials which are designed to show that the regimen under consideration has some activity or more
activity than the standard regimen-at least for some patients under some circumstances -and merits further study. In these studies it is efficient to focus on a group of patients who are likely to yield unambiguous information quickly (the group of patients in which the regimen should work best), such as chemotherapy naive patients who are receiving cisplatin. Measures of efficacy will depend on the specific questions for which the study is being designed. Usually, the goal is to obtain a yes or no answer: Is there activity for preventing acute vomiting? Is there activity against delayed vomiting? The second type of study is designed to evaluate the consequences of the proposed regimen if it were prescribed as standard therapy to some well-defined group of patients. The design for this study must (1) specify the measurements which best reflect efficacy, (2) establish the time frame in which efficacy will be assessed (delayed vs acute emesis at each course; nausea and vomiting on first vs subsequent courses), (3) identify the 'standard' or control treatment against which the regimen will be compared, and (4) define the target population (the group of patients to whom the conclusions will be extended). The precise questions to be answered by the trial will determine how the four above issues will be addressed by the design. Furthermore, the choice of the target population will determine the selection of patients for the trial. For example, in a trial of delayed emesis, the question could arise of whether to include patients who were failures of five or more emetic episodes) during the first 24 h following chemotherapy. If the goal of the trial is to assess the efficacy against delayed emesis in patients who were failures during the acute phase, then these patients must be included in the trial; if not, then patients who experienced five or more emetic episodes should not be included. Cross-over designs In general, cross-over designs will not be appropriate in antiemetic trials since the outcome during the first course of chemotherapy can have a moderate to large impact on the outcome during the second course. To illustrate this point, consider the example in Figure 4, in which two drugs are compared in a setting where the chemotherapy is very emetogenic. The first drug, Drug A, prevents all emetic episodes (vomiting and retching) in 50% of subjects-both during the first and second courses. Drug B controls vomiting and retching in 65% of patients during both the first and second courses. So for both the first and second course, Drug B protects an additional 15% of patients when compared to Drug A. For convenience, a patient who experiences no emetic episodes will be called a complete responder.
ANTIEMETIC STUDY DESIGN
S37
Table I Probability of no emesis during the second course of chemotherapy Probability of no emesis For Drug A:
DRUG A
NUMBER OF EMETIC EPISODES DURING FIRST COURSE
If no emesis occurred during first course: If one or more episodes occurred during first course:
0.33/0.50 = 0.66 0.17/0.50 = 0.34
For Drug B: If no emesis occurred during first course: If one or more episodes occurred during first course:
0.50/0.65 = 0.77 0.15/0.35 = 0.43
NUMBER OF EMETIC EPISODES DURING SECOND COURSE None
None 0.33
L90.17
1
.0 0.50
1+
0.17
0.50
.33 05 0.50
0.50
NUMBER OF EMETIC EPISODES DURING SECOND COURSE DRUG B NUMBER OF EMETIC EPISODES DURING FIRST COURSE
None
1+
None
1+
0.50 0.15
0.15
0.65
0.20
0.35
0.65
0.35
design would still require fewer subjects than the parallel subjects design but it is now no longer obvious that it would yield a major savings-at least in terms of the number of courses of treatment. While there may be some situations in which a cross-over design would be advantageous in an entiemetic trial, it should be the responsibility of the study investigators to convince themselves and critical reviewers, that occurrence of emesis during the second course of chemotherapy does not depend on events during the first course.
RANDOMISED TO DRUG A FIRST: NUMBER OF EMETIC EPISODES WITH DRUG A
Figure 4 Probability of no vs one or more emetic episodes during the first and second courses of chemotherapy for patients receiving anti-emetic drugs A and B.
NUMBER OF EMETIC EPISODES WITH DRUG B None 1+ 38 None 12 50 Nn 2 5 29 21 50 1+ 59 41
RANDOMISED TO DRUG B FIRST:
The important point is highlighted in Table I: during the second course, both of the drugs are more effective in patients who had no emetic episodes during the first course of therapy. For example with Drug A, 66% of patients who experienced no emesis during the first course also experience no emesis during the second course. In contrast, only 34% of patients who vomited or retched during the first course, were complete responders during the second course. Figure 5 presents the expected results in this situation, if a cross-over study with 200 patients were executed. One hundred patients would be randomised to receive Drug B during the first course and Drug A during the second course. One hundred patients would receive Drug A first and Drug B second. Overall 52.5% of subjects would experience a complete response when they received A, compared to 62% on B. The difference in complete response rates between the two drugs would decrease from 15% (as could be seen during the first course) to 9.5%. In Table II, sample sizes have been calculated. A 'conventional' parallel subject trial designed to achieve 80% power with a two-sided test would require 364 subjects (assuming no drop-outs) (Casagrande et al., 1978). An incorrectly planned cross-over design would claim to require only 111 subjects (Duffy, 1984). But with 11 1 subjects there would be only 41% power-not 80% power-to detect a difference of 9.5%. A cross-over design with the correct response rates and using a simple analysis (McNemar's test) would need 286 subjects, if they all completed two courses. The cross-over
NUMBER OF EMETIC EPISODES WITH DRUG B
NUMBER OF EMETIC EPISODES WITH DRUG A
None 1+
None 43 12 55
1+
22 23 45
65 43
PERCENT OF PATIENTS WITH COMPLETE PROTECTION: DRUG A: 100 x (50 + 55)/200 = 52.5% DRUG B: 100 x (59 + 65)/200 = 62.0%
Figure 5 Expected results of a trial utilising a cross-over design with the anti-emetic drugs A and B described in Figure 4.
Table II Sample size requirements for a parallel subjects design and cross-over designa
Study design Parallel subject:
Drug Drug A Drug B
Cross-over:
Drug A Drug B
Complete protection 50% 65% 50% 65%
Required Required number of number of subjects courses 364 364 111
222
Cross-over:
Drug A 52.5% 286 572 Drug B 62% aCalculations are based on a 2-sided test with 80% power and assume no drop-outs.
References
CASAGRANDE, J.T., PIKE, M.C. & SMITH, P.G. (1978). An improved approximate formula for calculating sample sizes for comparing two binomial distributions. Biometrics, 34, 483.
DUFFY, S.W. (1984). Asymptotic and exact power for the McNemar test and its analogue with R controls per case. Biometrics, 40, 1005.
S35-S37
©
Ltd., (D Press Ltd., Macmillan Macmillan Press
1992
1992~~~
Antiemetic study design: A discussion of Dr Olver's paper S. Groshen Department of Preventative Medicine, University of Southern California School of Medicine, Los Angeles, California, USA.
I would like to start by complimenting Dr Olver on a lucid and comprehensive paper. Since I quite agree with his comments, I will take the opportunity to expand on some of the issues he has briefly mentioned. The design of any clinical trial, not just an antiementic trial, should be largely determined by the goals and methods of the analysis, which in turn reflect the objectives of this study. Thus, I will begin by mentioning issues regarding the data analysis.
Role for multivariate analyses As Dr Olver and others have mentioned, the choice of measures of efficacy is one of the more challenging aspects of designing an antiemetic trial. Since we are concerned with several measures of efficacy in antiemetic trials (e.g. nausea, vomiting, and toxicity), we would benefit from examining these outcome measures jointly. Take as an example, the simple trial in which we have studied one antiemetic drug with two measures of efficacy, the number of episodes of vomiting within the first 24 h of chemotherapy administration and the number of hours that the patient felt nauseated during the same 24 h period. For purposes of this illustration, we will ignore side effects and assume that the patients and their chemotherapy are all relatively homogeneous. Suppose the results-univariately-are as given in Figures la and b. There are 40 patients; 50% have no emetic episodes and 30% experience no nausea. In Figures 2a and b two possible patterns of nausea and vomiting for the same 40 patients are plotted. We would draw different conclusions regarding the efficacy of this antiemetic drug, depending on whether the relationship between number of episodes and time nauseated resembled Figure 2a or Figure 2b. In the first example, 12 of the 40 patients experienced no emetic episodes and no nausea; an additional eight experienced only one-half hour of nausea. We might conclude that with this chemotherapy/antiemetic combination, 20/40 or 12/40 of the patients experience no or negligible nausea and no vomiting. On the other hand, in Figure 2b, all of the patients with no vomiting experienced at least one hour of nausea. Thus 100% of patients experienced some side effects to chemotherapy. This type of approachmultivariate analysis -will be necessary for understanding the overall effect of antiemetic agents.
Eligibility and evaluability criteria and analysis on an intent to treat basis Inclusion and exclusion criteria involve information which is available to the study co-ordinators BEFORE a patient is registered into the trial and (if appropriate) randomised. As Dr Olver has mentioned, these criteria should be objective, amenable to documentation, and unambiguous. All registered patients (registered for study participation, not to be confused with the separate registration which often takes place for screening) must be included and accounted for in the final analysis. The screening and registration process must be taken very seriously; this is the time during the trial when investigators have complete control. Once a patient is registered and treatment has started, the patient is usually classified as evaluable or not. The labels 'evaluable' or 'inevaluable' are based on information obtained after registration, assignment of treatment and usually, after start of treatment. A patient can be inevaluable
for two reasons: the measures of efficacy were not obtained or the patient was not 'adequately treated'. There is no satisfactory way to deal with patients missing their measurements of efficacy. We should assess the impact of these patients on the conclusions: include them as failures, include them as successes, and exclude them. If the results are consistent-that is, if the conclusions do not change-then we must report this and use the more conservative version of the analysis. If the conclusions are inconsistent, then this must be reported and a decision made as to whether or not the study should be repeated. If the treatment was inadequate or not done according to protocol, then this patient must be included in the results (with enough information given to allow the reader to evaluate the impact of excluding the subject). Thus, even though a study participant has been labelled 'inevaluable', outcome information must be measured and recorded for analysis. In a randomised study, we must analyse the results on an 'intent to treat' basis. If there are compelling reasons, we may decide to look at the data with the 'inevaluable' patients deleted and compare the conclusions. But our reference is always the 'intent to treat' analysis-i.e. we include ALL patients randomised and classify them according to the randomisation outcome. There are no easy solutions for dealing with inevaluable patients-the best strategy is to avoid the problem and, failing that, to document what has been done. A large number of inevaluable patients will compromise the impact and conclusions of any trial.
a (A
+.O CL a) o
0L
.0
E z
Number of emetic episodes
U)
a)
0.
0)
a) 0
0) E
CO
I0I
z
Number of hours of nausea Figure 1 a Distribution of patients according to the number of emetic episodes experienced during the 24 h after chemotherapy (total of 40 patients). b Distribution of patients according to the duration (in hours) of nausea during the 24 h after chemotherapy (total of 40 patients).
S. GROSHEN
S36
a
.
87en
um
100 PATIENTS
Course 2
CONTINUE TREATMENT 60 PATIENTS
Course 3
CONTINUE TREATMENT 36 PATIENTS
Course 4
CONTINUE TREATMENT 22 PATIENTS
a
MAJOR RESPONSE
:
6543-
Course 1
MAJOR
3+
3+
I
MAJOR
:u:::
o
-1-
-
TTT
-1
0
6 7 8 Number of emetic episodes 2
1
0
3
4
5
9
10
CA
b
0
A 00 ~~~ ~~~~~~ ~~~~~~~~~~~~ ~~~ ~~~
~~~
~~~
U,
76-
C3 5-
I
I*I-
43-
21I
-1V
II
-1
0
II
I
I
1
2
3
4
EMETIC EPISODES OFF-STUDY 14 PATIENTS
I
I
I
I
I
5
6
7
8
9
MAJOR RESPONSE
13 PATIENTS
3+
EMETIC EPISODES 9 PATIENTS
Figure 3 Evaluation of an anti-emetic agent over four courses of chemotherapy and the number of patients treated at each course. Major response = 0-2 emetic episodes during the 24 h after chemotherapy.
~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~
8a)
EMETIC EPISODES OFF-STUDY 24 PATIENTS
I
I
-1
3+
EMETIC EPISODES OFF-STUDY 40 PATIENTS
I
10
Number of emetic episodes Figure 2 a Distribution of patients (total 40) where the number of emetic episodes and duration of nausea (in hours) are positively correlated. b Distribution of patients (total 40) where the number of emetic episodes and duration of nausea (in hours) are inversely correlated.
Denominator in trials with multiple courses When we evaluate the antiemetic efficacy of a drug over several courses, the temptation is to include only those patients who begin each course in the analysis of subsequent courses. This can lead to very different and potentially misleading statements. Consider the example in Figure 3 where only subjects with a major response (0, 1 or 2 emetic episodes during the first 24 h) are given the same antiemetic agent in the next course of chemotherapy. Suppose that with this drug, 60% of subjects, who had a prior major response, have a major response at the current course-always. The expected results are: (1) at each course 60% of patients who NEVER had three or more emetic episodes, had a major response and (2) by the end of the fourth course, only 13% of patients were ALWAYS responders. Because the criteria for selecting and treating patients, on subsequent courses are usually different from the criteria for selecting them for the first course, care must be taken to describe the initial denominator (the number of patients who were treated at the first course) as well as the number of patients treated at each of the later courses. The denominator should be the number of patients, and not the number of courses.
Selection ofpatients for antiemetic studies Once doses and schedules have been chosen for a particular antiemetic drug or set of agents, based on animal studies and Phase I trials, trials to assess efficacy are planned. These efficacy trials fall, broadly, into two types. The first group includes those trials which are designed to show that the regimen under consideration has some activity or more
activity than the standard regimen-at least for some patients under some circumstances -and merits further study. In these studies it is efficient to focus on a group of patients who are likely to yield unambiguous information quickly (the group of patients in which the regimen should work best), such as chemotherapy naive patients who are receiving cisplatin. Measures of efficacy will depend on the specific questions for which the study is being designed. Usually, the goal is to obtain a yes or no answer: Is there activity for preventing acute vomiting? Is there activity against delayed vomiting? The second type of study is designed to evaluate the consequences of the proposed regimen if it were prescribed as standard therapy to some well-defined group of patients. The design for this study must (1) specify the measurements which best reflect efficacy, (2) establish the time frame in which efficacy will be assessed (delayed vs acute emesis at each course; nausea and vomiting on first vs subsequent courses), (3) identify the 'standard' or control treatment against which the regimen will be compared, and (4) define the target population (the group of patients to whom the conclusions will be extended). The precise questions to be answered by the trial will determine how the four above issues will be addressed by the design. Furthermore, the choice of the target population will determine the selection of patients for the trial. For example, in a trial of delayed emesis, the question could arise of whether to include patients who were failures of five or more emetic episodes) during the first 24 h following chemotherapy. If the goal of the trial is to assess the efficacy against delayed emesis in patients who were failures during the acute phase, then these patients must be included in the trial; if not, then patients who experienced five or more emetic episodes should not be included. Cross-over designs In general, cross-over designs will not be appropriate in antiemetic trials since the outcome during the first course of chemotherapy can have a moderate to large impact on the outcome during the second course. To illustrate this point, consider the example in Figure 4, in which two drugs are compared in a setting where the chemotherapy is very emetogenic. The first drug, Drug A, prevents all emetic episodes (vomiting and retching) in 50% of subjects-both during the first and second courses. Drug B controls vomiting and retching in 65% of patients during both the first and second courses. So for both the first and second course, Drug B protects an additional 15% of patients when compared to Drug A. For convenience, a patient who experiences no emetic episodes will be called a complete responder.
ANTIEMETIC STUDY DESIGN
S37
Table I Probability of no emesis during the second course of chemotherapy Probability of no emesis For Drug A:
DRUG A
NUMBER OF EMETIC EPISODES DURING FIRST COURSE
If no emesis occurred during first course: If one or more episodes occurred during first course:
0.33/0.50 = 0.66 0.17/0.50 = 0.34
For Drug B: If no emesis occurred during first course: If one or more episodes occurred during first course:
0.50/0.65 = 0.77 0.15/0.35 = 0.43
NUMBER OF EMETIC EPISODES DURING SECOND COURSE None
None 0.33
L90.17
1
.0 0.50
1+
0.17
0.50
.33 05 0.50
0.50
NUMBER OF EMETIC EPISODES DURING SECOND COURSE DRUG B NUMBER OF EMETIC EPISODES DURING FIRST COURSE
None
1+
None
1+
0.50 0.15
0.15
0.65
0.20
0.35
0.65
0.35
design would still require fewer subjects than the parallel subjects design but it is now no longer obvious that it would yield a major savings-at least in terms of the number of courses of treatment. While there may be some situations in which a cross-over design would be advantageous in an entiemetic trial, it should be the responsibility of the study investigators to convince themselves and critical reviewers, that occurrence of emesis during the second course of chemotherapy does not depend on events during the first course.
RANDOMISED TO DRUG A FIRST: NUMBER OF EMETIC EPISODES WITH DRUG A
Figure 4 Probability of no vs one or more emetic episodes during the first and second courses of chemotherapy for patients receiving anti-emetic drugs A and B.
NUMBER OF EMETIC EPISODES WITH DRUG B None 1+ 38 None 12 50 Nn 2 5 29 21 50 1+ 59 41
RANDOMISED TO DRUG B FIRST:
The important point is highlighted in Table I: during the second course, both of the drugs are more effective in patients who had no emetic episodes during the first course of therapy. For example with Drug A, 66% of patients who experienced no emesis during the first course also experience no emesis during the second course. In contrast, only 34% of patients who vomited or retched during the first course, were complete responders during the second course. Figure 5 presents the expected results in this situation, if a cross-over study with 200 patients were executed. One hundred patients would be randomised to receive Drug B during the first course and Drug A during the second course. One hundred patients would receive Drug A first and Drug B second. Overall 52.5% of subjects would experience a complete response when they received A, compared to 62% on B. The difference in complete response rates between the two drugs would decrease from 15% (as could be seen during the first course) to 9.5%. In Table II, sample sizes have been calculated. A 'conventional' parallel subject trial designed to achieve 80% power with a two-sided test would require 364 subjects (assuming no drop-outs) (Casagrande et al., 1978). An incorrectly planned cross-over design would claim to require only 111 subjects (Duffy, 1984). But with 11 1 subjects there would be only 41% power-not 80% power-to detect a difference of 9.5%. A cross-over design with the correct response rates and using a simple analysis (McNemar's test) would need 286 subjects, if they all completed two courses. The cross-over
NUMBER OF EMETIC EPISODES WITH DRUG B
NUMBER OF EMETIC EPISODES WITH DRUG A
None 1+
None 43 12 55
1+
22 23 45
65 43
PERCENT OF PATIENTS WITH COMPLETE PROTECTION: DRUG A: 100 x (50 + 55)/200 = 52.5% DRUG B: 100 x (59 + 65)/200 = 62.0%
Figure 5 Expected results of a trial utilising a cross-over design with the anti-emetic drugs A and B described in Figure 4.
Table II Sample size requirements for a parallel subjects design and cross-over designa
Study design Parallel subject:
Drug Drug A Drug B
Cross-over:
Drug A Drug B
Complete protection 50% 65% 50% 65%
Required Required number of number of subjects courses 364 364 111
222
Cross-over:
Drug A 52.5% 286 572 Drug B 62% aCalculations are based on a 2-sided test with 80% power and assume no drop-outs.
References
CASAGRANDE, J.T., PIKE, M.C. & SMITH, P.G. (1978). An improved approximate formula for calculating sample sizes for comparing two binomial distributions. Biometrics, 34, 483.
DUFFY, S.W. (1984). Asymptotic and exact power for the McNemar test and its analogue with R controls per case. Biometrics, 40, 1005.
