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Interpretation of cancer prevention trials
PREVENTIVE
MEDICINE
18,
721-731 (1989)
Interpretation
of Cancer
Prevention
Trials’S2
THOMASE. MOON, PH.D. Arizona Cancer Center, 1515 North Campbell Avenue, Tucson, Arizona 85724 Principles and methods to guide interpretation require a different emphasis for cancer trials. Assumptions used to design a trial must be validated and modified during the trial to avoid limitations. To maximize information from such trials, recruitment strategies for commonly free-living subjects, measurement of safety and compliance, and ascertainment with pathologic review of endpoints must be obtained. Consideration of multiple endpoints may provide a better interpretation of cancer prevention for skin, colon, and transient occurrences illustrated by cervical dysplasia or biochemical precursors. A careful definition of the limitations of preventive trials is required. These include the actual size of the intervention groups, completeness and duration of follow-up, and comparison between trial participants and a defined source population. To obtain a valid interpretation with adequate precision of intervention effectiveness, time to endpoints should be evaluated using statistical multivariate methods such as Cox proportional hazard or relative risk models. These permit adjustment for important confounding and risk modifiers such as compliance, dietary intake, and drift in control group. The magnitude of the intervention efftcacy and the generalizability of results of the trial will be negatively impacted if the intervention has a delayed (latent) effect. Such delay in intervention effect requires added considerations with possible extension of trial duration. Use of confidence limits for intervention effectiveness provides added insight and improved interpretation of prevention trials. The final component of a cancer prevention trial, as with any study, is to interpret and report its results. Providing a valid interpretation with adequate precision to hypotheses of a cancer prevention trial requires added emphasis on the accuracy of the assumptions made to design the trial and the duration of the trial. Design assumptions regarding compliance to the prescribed interventions, time until the experimental intervention achieves full effect, and the frequency of endpoints directly impact on the number of endpoints observed. Terminating a cancer prevention trial before adequate information is obtained, thus severely flawing its interpretation, requires ongoing awareness. Interpretation of a cancer prevention trial should include several added steps: first, investigators to critically review the actual manner in which the trial was conducted; second, carry out an appropriate analysis of the data; and third, review the results and note exceptions or limitations in the data. The results of the trial should be contrasted with previous studies. Implications of the results to future trials should be considered. Finally, these interpretations should be documented in a written report and made available to the SCientifiC
COITIIIIUnity.
0 1989 Academic
Press, Inc.
The primary purpose of this article is to emphasize the internal and external aspects of the interpretation that particularly relates to cancer prevention trials (Tables 1 and 2). The integral relationship of the data analysis to the interpretation of a trial and the reporting of the results is also presented. For illustration, refer’ Presented at the Third International Conference on the Prevention of Human Cancer: Chemoprevention, Tucson, AZ, January 12-15, 1988. ’ Sponsored by research grants from the Arizona Disease Control Research Commission (8277OOOOOO-l-O-258042) and the National Institutes of Health, U.S. Department of Health and Human Services (CA34256, CA27502, CA23074). 721 0091-7435/89$3.00 Copyright 8 1989 by Academic Press, Inc. All rights of reproduction in any form reserved.
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ence will be made to two ongoing cancer prevention trials of retinoids to reduce the risk of skin cancer that Norman Levine, M.D., my co-principal investigator at the University of Arizona, and I have had the opportunity to direct. These were the first comparative intervention trials initiated at the University of Arizona: the trial of retinol (25,000 W/day) vs placebo in subjects with a history of at least 10 actinic keratoses (AK), and a second trial evaluating retinol (25,000 III/day), isotretinoin (5 or 10 mg/day) vs placebo in subjects with at least 4 prior basal cell or squamous cell carcinomas (BCCECC). INTERNAL ASPECTS Three aspects of the internal conduct and interpretation of cancer prevention trials deserve special consideration: first, the actual conduct of the trial; second, the analysis of data from the trial; and third, use of confidence limits. Was Trial Conducted as Designed?
The interpretation of a trial should take into consideration how it was actually conducted and changes that occurred during the trial. This will help ensure the scientific integrity of the trial to provide a valid conclusion: either a definitive conclusion that the intervention has reduced the cancer risk or an informative null result that no substantial risk reduction was provided by the intervention. A clear statement of hypotheses is required of all trials but requires added emphasis for cancer prevention trials due to the multiplicity of endpoints. The primary hypotheses of the effect of the intervention in reducing the cancer risk are often clearly stated and the foundation of the trial design. In contrast, secondary hypotheses that relate to other key endpoints, including safety of the intervention and compliance to the prescribed intervention, should also be clearly stated. In the skin cancer prevention trials, the comparison of type and degree of side effects in the placebo vs the retinoid groups was a corresponding secondary hypothesis. This was believed to be important due to the enrollment of generally free-living TABLE 1 INTERPRETATION OF CANCER PREVENTION TRIALS: INTERNAL ASPECTS
Was trial conducted as designed? Hypotheses Sample size/endpoints Subjects Recruitment Intervention Assignment method Compliances/safety Confounding factors Follow-up Analyses Planned evolved risk factors/interrelationship Time trends Latent effect Confidence limits
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TABLE 2 INTERPRETATION OF CANCER PREVENTION TRIALS: EXTERNAL ASPECTS
Generalizability of results Volunteers Defined populations Effectiveness versus efficacy Comparison to other studies Reporting results
study subjects, and the spectrum of cutaneous and other side effects previously reported for retinoids, albeit at substantially higher doses. Other secondary hypotheses relate to the methods used to measure compliance in the intervention groups and the effect of motivating compliance. Post hoc hypotheses, developed after the trial was initiated and often after interim analyses has occurred, must be defined and clearly stated as hypotheses generated by the trial and thus not to be conclusively answered by the trial. The assumptions used during the design of the trial should be compared with the observed data from the trial. Not only should the target number of subjects that was part of the trials design be compared with the number of subjects actually enrolled but the total number of endpoints targeted and observed should be compared. Longer follow-up commonly results in the accumulation of more endpoints for cancer prevention trials. Thus, extending the duration of follow-up and accumulating added endpoints may address discrepancies in the targeted number of endpoints anticipated and the actual number needed. The common observation that volunteers for disease prevention trials have lower morbidity and mortality than the general population (i.e., health volunteer effect) may result in longer follow-up to obtain the targeted number of endpoints. For example, the 3% annual decline in cardiovascular mortality for the U.S. population observed during the conduct of the Multiple Risk Factor Intervention Trial (MRFIT) resulted in fewer endpoints than expected in the control group and reduced power to evaluate the primary hypothesis (1). Increased follow-up could have addressed that anticipated issue. Subject drop-in and drop-out can have a significant impact on the sample size actually required for a cancer prevention trial. While it is recommended that drop-in and drop-out be considered in the sample size calculation, differences between the assumed and observed frequency of subjects that drop-in or drop-out of the trial must be considered with corresponding changes in sample size during the conduct of the trial. Methods have been published that demonstrate the impact of compliance on statistical power and the recalculation of sample size (2, 3). Strategies to recruit study subjects should be clearly defined, including how potentially eligible people are informed of the trial, as well as the entry and exclusion criteria. Strategies may change from the time the trial is designed and are subject to change throughout the conduct of the trial. For example, recruitment for the SKICAP trials was planned to be exclusively through dermatologists in the Tucson metropolitan area. This plan was effective during the first year of recruitment. More recently decreased enrollment has resulted in the use of other
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strategies, including the use of the print, TV, and radio media to inform potentially eligible subjects of the trial and the need for additional volunteer participants. Also, enrollment was expanded from one to four different communities. Many prevention trials recruit free-living individuals who have minimal or no ongoing clinical care. Thus strategies such as those used in the SKICAP trials that are cost effective and directly inform potential subjects need further development and evaluation of their impact on the generalizability of the trial. Our experience to date indicates that approximately 50% of all persons who show interest in participating were scheduled for screening at one of the enrolling clinics, approximately 25% of all persons met entry criteria and were accrued into the run-in period, with 75-80% of those accrued going on to be enrolled and randomly assigned to one of the intervention groups. Thus, approximately 20% of all persons who show an interest in participating in the SKICAP trials meet the defined recruitment criterion and are enrolled. This percentage appears to be higher than that reported for other disease prevention trials. The definition of the intervention should include its type, dose, and dose rate. Changes in any part of the intervention that occur during the course of trial require complete description. In designing the SKICAP trial for AK subjects, isotretinoin was the retinoid originally planned as the experimental agent. However, shortly after beginning subject accrual, the pharmaceutical supplier chose to withdraw the availability of isotretinoin from the SKICAP trial. Retinol and retinol placebo were substituted after documentation of adequate rationale. Fortunately the change in the experimental agent occurred when all subjects were on the placebo run-in phase and no subject had been randomly assigned to the experimental or placebo group. The resulting change in retinoid for the SKICAP trial in AK subjects did result in unavoidable confusion among some subjects and a short delay in the trial. Far more deleterious effects on the interpretation of the trial would have occurred if a change in experimental agent had occurred later in the trial. Intervention assignment and blinding require careful consideration during the trial design and after the trial is initiated. Stratification factors, including inclusion and exclusion criteria, and how they may have changed during the conduct of the trial will provide better understanding of how the trial was actually carried out. Also, the completeness of the blinding of subjects, clinic staff, and referring physicians should be evaluated. Prior to the initiation of the SKICAP trials, some of the cooperating dermatologists indicated that they might be able to determine which subjects were taking the assigned retinoid due to anticipated cutaneous side effects. The importance of maintaining subject blindness has been repeatedly emphasized to all referring dermatologists. A recent survey indicated that cutaneous side effects observed by dermatologists were not extreme enough to provide an easy indicator of which subjects were in fact taking retinoids. Thus, SKICAP dermatologists have not been blinded as they had anticipated. Another example of the success of maintaining the blind nature of the trial relates to the placebo used in the SKICAP trials. One subject reported that he had attempted unsuccessfully to determine whether he was assigned retinoid or placebo. The
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subject had requested information of his pharmacist as to the appearance and content of the capsules provided by SKICAP staff. Fortunately, the pharmacists indicated that the capsules looked in all ways like retinoid capsules. A point to be learned from these experiences that may relate to many blinded intervention trials is that an apparently well-designed plan to keep the trial double-blind can be undermined by the referring medical staff or the subjects. The degree of unblinding should be determined and reported. Compliance to the prescribed intervention is critical to the success of a disease prevention trial and is markedly complex to measure and motivate. Measurement of compliance could use a variety of subjective or objective methods. Limitations in resources, subject tolerance, and fundamentaal knowledge of human behavior have resulted in pragmatic choices regarding compliance methods used in the current generation of cancer prevention trials. To obtain an estimate of compliance for each subject participating in the SKICAP trials, three subjective methods have consistently been used. The primary measure of compliance has been the number of capsules returned by the subject at each follow-up visit. Other measures include the subjects recording on a monthly calendar form the time each day they take their capsule and the number of capsules reported as not taken during randomly selected 7-day periods. While all three methods were highly correlated and indicated that over 90% of study subjects were complying with the intervention, validation of the subject’s self-report was desired. Compliance was objectively estimated using a biologic marker (10 mg riboflavin combined with the retinoid capsules) and a computerized pill blister pack. The pill pack was developed in collaboration with Seth Eisen, M.D., from Washington University, and electronically records the time and date that each blister was opened. Each of the objective methods to measure compliance were highly correlated to the pill count method and indicated that subjects were accurately and consistently reporting their compliance to the prescribed intervention. Methods used to motivate compliance including the type, frequency, and uniformity of application require added consideration. The use of a run-in period to assess the likelihood of long-term compliance prior to random assignment of the intervention may be extremely useful in identifying a compliant cohort. Even though such run-in periods may be carefully carried out prior to random allocation, the proportion of subjects that drop-out or drop-in to a trial after random assignment will have substantial reduction on the power. Thus, to ensure an adequate interpretation of the trial by ensuring adequate power, the number of endpoints may require to be changed (commonly increased) prior to terminating a trial. A change in the number of endpoints can be commonly accomplished by increasing the total sample size or extending trial follow-up. In addition to reports of compliance by the subject, other markers of compliance have been investigated, including subject characteristics such as demographic, social, economic, and behavioral factors, and frequency and degree of side effects. The interrelationship between subject characteristic and compliance to date has not provided a well-defined motivational plan that directly results in high compliance among all or nearly all subjects. While further compliance re-
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search is needed, cost considerations and potential dilution of the ability to answer the primary hypothesis need to be balanced. A valid estimate of subject compliance may be minimally essential to the interpretation of a trial. Improved understanding of the relationship between compliance and safety during a cancer prevention trial may result from an inadequate interpretation of the data. The spectrum of side effects known or anticipated prior to the start of a trial should be monitored and updated during the conduct of the trial. How safe was the experimental intervention? Was the blind nature of the trial affected? These are two key questions that influence the interpretation of a trial. The plan to use retinoids in the SKICAP trials resulted in an extensive clinical and pathological monitoring of subjects with ongoing review by two extramural safety monitoring committees. The continuation of the trials indicates that side effects have not been different than anticipated and adequately tolerated using the modest dose of retinoids. How endpoints were defined, measured, and verified during the actual conduct of the trial will have an impact on study interpretation. The requirement for pathologically confirmed diagnosis of invasive cancer is commonly used for most of the ongoing cancer chemoprevention trials. Next generation cancer prevention trials may successfully utilize biochemical or other intermediate endpoints. The biologically valid relationship between the intermediate endpoint and the cancer endpoint will clearly have an impact on the interpretation of such intermediate endpoints and thus the effectiveness of the intervention. One of the potential interpretations derived from the current generation of cancer chemoprevention trials is the potential to identify and begin to validate such a relationship. Risk factors that are putatively related to study endpoints again are commonly well defined during the design phase and measuredduring the conduct of the trial. An adequate interpretation of the trial would include the actual magnitude of the risk factor. This should not only include confounding factors such as age or gender but also event modifiers which have differing magnitudes of effect on different subsets of the study population. One example of such event modifiers is an assessmentof dietary intake of key micro- and macronutrients. It may not be adequate to simply consider such dietary factors as simple confounders, but a careful assessmentof their role as an event modolier should be included in the interepretation of the trial. Follow-up may be classified as one of the most important aspects of a cancer prevention trial. Without sulficient follow-up, there will be inadequate numbers of endpoints and insufficient power to evaluate the hypotheses. Frequency of followup should be considered, particularly whether follow-up procedures were equally applied to both the experimental and control groups. A key question is whether the duration of follow-up has been sufficient to adequately discriminate between two markedly different interpretations of the study: first, the situation in which the experimental intervention did not markedly reduce the risk of cancer and second, the experimental intervention was not fully efftcacious for some latent period. For example, the benefits of stop smoking might be interpreted as ineffective in lowering the risk of lung cancer in heavy smokers if the duration of follow-up was not less than 2 years. A decrease in risk begins to appear after 2
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years with a follow-up duration of 9 years required before maximal decrease is observed (4). Analyses
Analysis of the data from a cancer prevention trial is a critical part of the complete interpretation of the trial. There may be differing and possibly competing analysis procedures that might be carried out. A key question as to whether different analyses yield different results must be carefully considered in the interpretation. The intention to treat philosophy suggests that all patients once randomized should be analyzed. An alternate method of analysis would be to include only a subset of “evaluable” subjects in the analysis. Such a subset might be defined by considering a certain dose level or compliance required in order for a subject to be included in the analysis. Critical comments have been appropriately expressed regarding such subset analyses (5). Interpretation of the data will benefit from a careful separation between the methods used to evaluate the primary hypotheses and statistical methods used to evaluate secondary or tertiary hypotheses which may be more effectively addressed in subsequent trials, A multitude of statistical methods are available for the analysis and comparison of intervention groups. Statistical methods deserving consideration include first, those using the frequency of events at a particular time point after the trial has begun (e.g., 5 years); second, the use of the proportional hazards model to address both the occurrence and the duration of time until endpoints occur, and third, use of relative risk methods recently proposed by Prentice (6). Each of the methods noted can accommodateadjustment for multiple risk factors. Of particular interest and somewhat more characteristic of cancer prevention trials is the occurrence of multiple endpoints for an individual subject. For example, in cancers of the skin, colon, or cervix it is possible and often likely that not one but multiple tumors or precancerous lesions may be diagnosed. In addition, the use of biochemical or other intermediate tumor markers may include a natural history of progression followed by regression and subsequently followed by progression. The occurrence of multiple endpoints provides new opportunities to include this additional information in the analysis in hopes of providing a better interpretation of trial data. The validity of the analysis and corresponding interpretation of the trial may be affected by which risk factors one considers in the analysis, including both causal as well as preventive factors. For example, the dose of a carcinogen such as ultraviolet light for skin cancer would be included in the multivariate analysis for the SKICAP trials. Of possible equal importance is the inclusion of preventive factors such as dietary nutrients other than vitamin A that should be considered. A key to this consideration and the validity of the analysis is how these causal and preventive factors are included in the analysis and whether they should be considered as risk modifiers (interaction terms) in the multivariate analysis. At this present state of the conduct and analysis of cancer prevention trials, it is difXcult at best to determine which, if any, and in what form such preventive factors should be included in the planned analysis of the data. It may be more appropriate to consider this a secondary analysis and include different mathematical func-
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tional forms of the causal and preventive factors in the analysis. Such an approach may lead to different results and require careful interpretation and reporting of trial data. The distribution of subject characteristics at the time they enter a trial may change during the enrollment period. This is of interest especially in a prevention trial because of the large number of subjects commonly required and the likelihood of enrollment lasting for several years. It would be of interest to analyze the change over time of the distribution of entry characteristics and the distribution of endpoints. During the first few months of a cancer prevention trial subjects may be recruited from an existing prevalent pool of eligible subjects; however, continued subject recruitment may come from subjects who have recently achieved the eligibility criteria. For example, in the SKICAP-BCC/SCC trial, there was an identified prevalent pool of persons that met eligibility criteria at the time the protocol was designed, approximately 2 years before the trial was actually initiated. Many of the people had a history of more than eight skin cancers. Consenting subjects from the prevalent pool were enrolled in the SKICAP trial during the first 12 months of enrollment. After which subjects were enrolled as they were diagnosed with the minimal number of requisite skin cancers to meet eligibility criteria. Thus, the time to the occurrence of their next skin cancer may differ as to the carcinogenesis stage as reflected by their skin cancer history. Delay in the preventive action or latent effect of the experimental intervention requires careful evaluation during the analysis of a cancer prevention trial. The impact of a latent effect, the resulting reduction in statistical power, and the corresponding requirement for an increase in the number of endpoints has been reported previously (2). While yet undetermined, it appears reasonable and prudent to assume that an extended period of carcinogenic exposure such as sunlight exposure may not be immediately reversed by an experimental chemoprevention or other intervention. Considering that subjects participating in a cancer prevention trial do not and often cannot totally eliminate their carcinogenic exposure it may be appropriate to assume that a cancer preventive agent will not demonstrate its full effect before 2 or 3 years of participation on the trial. A cancer prevention trial planned for a 3-year median follow-up of all study subjects may be severely limited in its ability to adequately answer the null hypothesis if the latent period is at least 1 year in duration. A careful analysis of a trial would not only estimate compliance of subjects participating in each of the intervention groups but also the presence and duration of a latent effect. As both of these issues can substantially reduce the statistical power of the trial, adjustment of sample size or study duration should be carried out prior to the termination of the trial. Confidence Limits
Use of confidence limits has been suggested by numerous authors as a method to improve the interpretation of a trial (7). Added emphasis appears to be appropriate for use of confidence limits to estimate the range of cancer risk reduction due to the experimental intervention that is consistent with the data. The requisite number of endpoints should be adequate to yield the indicated statistical power planned during the design of the trial. The maximum and minimum effect of the
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experimental intervention obtained from a confidence interval may improve the interpretation of a prevention trial. EXTERNALASPECTS External aspects of the interpretation of a prevention trial include the generalizability of the results of the trial, consideration of the efficacy of the intervention, comparison of trial results to other studies, and the reporting of the results of the trial. External aspects should receive added emphasis for cancer prevention trials due to the small number of Phase III-V trials to be carried out for specific types of cancer or interventions. Generalizability of Results Generalizability is the one aspect that most authors are reluctant to fully discuss but the one area that most readers of the published report of a trial are eager to interpret. Because the investigator is in the best position to know the advantages and limitations of the prevention trial, adequate interpretation including its generalizability should be provided. However, limitations do exist in the ability of the investigator to generalize the results of the trial. For example, generalizing the results of a trial with high risk subjects is difficult at this early stage of cancer prevention research. It is unclear if such a generalization is appropriate or what limitations may apply. One aspect of the generalizability of a prevention trial is how the subjects relate to a defined population. Subjects participating in a trial or any type of research are volunteers and may not be a randomly selected sample from a defined population. The reference frame for the study subjects may have been a geographic area, occupational group, or a medical clinic. For example, SKICAP participants include volunteers from the Tucson and Phoenix metropolitan areas. In contrast participants from an enrolling clinic in San Diego, California, are volunteers from one specific dermatologic clinic. Interpretation and generalizability of a prevention trial may be improved if the participants are compared with a defined population. Use of a population-based cancer registry may provide one available comparison group. Comparison of the registry population with subjects from the placebo (control) group that are diagnosed with cancer during the trial would indicate the similarity between the two groups for available risk factors. Unfortunately, it is not common for cancer risk factors to be abstracted as part of a cancer registry. Another alternative for comparison may be persons selected as controls for a population-based cancer etiology case-control study or as population-based subjects selected for participation in a cohort study. The recent initiation of a pair of skin cancer case-control studies in Southeastern Arizona that include a randomly selected populationbased control group is one example of a representative sample from a defined population that will be used for comparison with the ongoing SKICAP trials. The extensive risk factor information collected from the control group will be used for comparison with the distribution of factors for SKICAP participants. Such a procedure will not only provide a comparison of risk factors for the cancer type of primary interest but also provide some indication of the possible magnitude of a healthy volunteer effect that is commonly seen in many medical research trials.
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Effectiveness
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vs Efficacy
Efficacy is commonly defined as the effect of an intervention if total compliance to the prescribed protocol was achieved by all participants. Most prevention trials are not able to measure efficacy directly as participant compliance is often less than complete. Effectiveness of an intervention is the often achievable measure of effect that is influenced by the level of compliance each participant actually achieves during a trial. Although the comparison of efficacy between experimental and control interventions is the goal of a cancer prevention trial, the often achievable measure is the comparison of the difference between the effectiveness of the interventions. Though not often able to be measured directly, the difference in efficacy may be estimated if the level of compliance can be separately quantified for each of the intervention groups. An estimate of intervention efftcacy may be obtained, using one of several published methods (8,9) and the study-derived estimates of intervention effectiveness and compliance. Such a measure may provide improved interpretation and ability to compare with similar measures from other prevention trials. Comparison
to Other Studies
The impact of a specific cancer prevention trial on the control of cancer in a general population is, at best, difficult to determine. The example of the changing dietary, exercise, and smoking behavior of the U.S. population may not be easily related to one or even a group of trials. It is more likely the composite of research, including descriptive, analytic, and experimental epidemiology studies, plus professional recommendations and the individual’s judgment to adopt the recommended intervention. The generalizability of an individual cancer prevention trial and its integration into the composite of prevention strategies may be assisted by the use of metaanalysis. Extensively used for a number of years by social scientists, the use of metaanalysis in public health to obtain an integrated interpretation of a collection of research papers is becoming acceptable (10). Long-term follow-up of the participants in a prevention trial may not only provide an adequate number of endpoints to answer the primary hypothesis but important additional information that could be valuable for improved interpretation and comparison between numerous prevention trials. For example, long-term behavioral changes in the participants to adapt the prescribed intervention plus information on the type, severity, and frequency of side effects can provide important new information for the planning of community intervention trials. For example, the Phase III SKICAP trials might be extended in follow-up and be redefined as a Phase II methodology trial evaluating the above-noted issues of compliance and safety as well as providing commonly unavailable information regarding diffusion of research findings throughout a community. Reporting
Results
An integral component of the interpretation of a prevention trial like all research studies is a careful reporting of the results of the trial. The investigator is truly in the best position to know the strength and weakness of the trial and should have
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the obligation to report these plus the discussion of the generalizability of the trial results. The publication of trial results and their interpretation provides one’s peers with the opportunity to evaluate and integrate the findings into the next generation of prevention trials. Such reporting also provides the necessary scientific foundation on which to develop the community recommendations and their relative cost effectiveness for disease prevention. REFERENCES 1. Multiple Risk Factor Intervention Trial Research Group. Multiple risk factor intervention trial: Risk factor changes and morbidity results. JAMA 1982; 248:1465-1474. 2. Moon TE. Clinical trials of cancer prevention agents: True versus observed prevention effects. Sfat Med 1986; 5435-439. 3. Donner A. Approaches to sample size estimation in the design of clinical trials-A review. Star Med 1984; 3:199-214. 4. Doll R, Peto R. Cigarette smoking and bronchial carcinoma: Dose and time relationship amongst regular smokers and lifetime non-smokers. .I Epidemiol Commun Health 1978; 32:303. 5. Byar D, Simon RM, Friedewald WT, et al. Randomized clinical trials: Perspective of some recent ideas. N Engl .I Med 1976; 295:74-80. 6. Prentice R, Mason MW. On the application of linear relative risk models. Biometrics 1986; 42~109-120. 7. Rothman K. Modem Epidemiology. Boston: Little, Brown, 1986:119-350. 8. Lachin JM. Introduction to sample size determination and power analysis for clinical trials. Controlled Clin Trials 1981; 2:93-l 14. 9. Wu M, Fisher M, DeMets D. Sample sizes for long-term medical trial with time-dependent dropout and event rates. Controlled Clin Trials 1980; 1:109-121. 10. Louis TA. Findings for public health from meta-analysis. Annu Rev Public Health 1985; 61-20.
MEDICINE
18,
721-731 (1989)
Interpretation
of Cancer
Prevention
Trials’S2
THOMASE. MOON, PH.D. Arizona Cancer Center, 1515 North Campbell Avenue, Tucson, Arizona 85724 Principles and methods to guide interpretation require a different emphasis for cancer trials. Assumptions used to design a trial must be validated and modified during the trial to avoid limitations. To maximize information from such trials, recruitment strategies for commonly free-living subjects, measurement of safety and compliance, and ascertainment with pathologic review of endpoints must be obtained. Consideration of multiple endpoints may provide a better interpretation of cancer prevention for skin, colon, and transient occurrences illustrated by cervical dysplasia or biochemical precursors. A careful definition of the limitations of preventive trials is required. These include the actual size of the intervention groups, completeness and duration of follow-up, and comparison between trial participants and a defined source population. To obtain a valid interpretation with adequate precision of intervention effectiveness, time to endpoints should be evaluated using statistical multivariate methods such as Cox proportional hazard or relative risk models. These permit adjustment for important confounding and risk modifiers such as compliance, dietary intake, and drift in control group. The magnitude of the intervention efftcacy and the generalizability of results of the trial will be negatively impacted if the intervention has a delayed (latent) effect. Such delay in intervention effect requires added considerations with possible extension of trial duration. Use of confidence limits for intervention effectiveness provides added insight and improved interpretation of prevention trials. The final component of a cancer prevention trial, as with any study, is to interpret and report its results. Providing a valid interpretation with adequate precision to hypotheses of a cancer prevention trial requires added emphasis on the accuracy of the assumptions made to design the trial and the duration of the trial. Design assumptions regarding compliance to the prescribed interventions, time until the experimental intervention achieves full effect, and the frequency of endpoints directly impact on the number of endpoints observed. Terminating a cancer prevention trial before adequate information is obtained, thus severely flawing its interpretation, requires ongoing awareness. Interpretation of a cancer prevention trial should include several added steps: first, investigators to critically review the actual manner in which the trial was conducted; second, carry out an appropriate analysis of the data; and third, review the results and note exceptions or limitations in the data. The results of the trial should be contrasted with previous studies. Implications of the results to future trials should be considered. Finally, these interpretations should be documented in a written report and made available to the SCientifiC
COITIIIIUnity.
0 1989 Academic
Press, Inc.
The primary purpose of this article is to emphasize the internal and external aspects of the interpretation that particularly relates to cancer prevention trials (Tables 1 and 2). The integral relationship of the data analysis to the interpretation of a trial and the reporting of the results is also presented. For illustration, refer’ Presented at the Third International Conference on the Prevention of Human Cancer: Chemoprevention, Tucson, AZ, January 12-15, 1988. ’ Sponsored by research grants from the Arizona Disease Control Research Commission (8277OOOOOO-l-O-258042) and the National Institutes of Health, U.S. Department of Health and Human Services (CA34256, CA27502, CA23074). 721 0091-7435/89$3.00 Copyright 8 1989 by Academic Press, Inc. All rights of reproduction in any form reserved.
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ence will be made to two ongoing cancer prevention trials of retinoids to reduce the risk of skin cancer that Norman Levine, M.D., my co-principal investigator at the University of Arizona, and I have had the opportunity to direct. These were the first comparative intervention trials initiated at the University of Arizona: the trial of retinol (25,000 W/day) vs placebo in subjects with a history of at least 10 actinic keratoses (AK), and a second trial evaluating retinol (25,000 III/day), isotretinoin (5 or 10 mg/day) vs placebo in subjects with at least 4 prior basal cell or squamous cell carcinomas (BCCECC). INTERNAL ASPECTS Three aspects of the internal conduct and interpretation of cancer prevention trials deserve special consideration: first, the actual conduct of the trial; second, the analysis of data from the trial; and third, use of confidence limits. Was Trial Conducted as Designed?
The interpretation of a trial should take into consideration how it was actually conducted and changes that occurred during the trial. This will help ensure the scientific integrity of the trial to provide a valid conclusion: either a definitive conclusion that the intervention has reduced the cancer risk or an informative null result that no substantial risk reduction was provided by the intervention. A clear statement of hypotheses is required of all trials but requires added emphasis for cancer prevention trials due to the multiplicity of endpoints. The primary hypotheses of the effect of the intervention in reducing the cancer risk are often clearly stated and the foundation of the trial design. In contrast, secondary hypotheses that relate to other key endpoints, including safety of the intervention and compliance to the prescribed intervention, should also be clearly stated. In the skin cancer prevention trials, the comparison of type and degree of side effects in the placebo vs the retinoid groups was a corresponding secondary hypothesis. This was believed to be important due to the enrollment of generally free-living TABLE 1 INTERPRETATION OF CANCER PREVENTION TRIALS: INTERNAL ASPECTS
Was trial conducted as designed? Hypotheses Sample size/endpoints Subjects Recruitment Intervention Assignment method Compliances/safety Confounding factors Follow-up Analyses Planned evolved risk factors/interrelationship Time trends Latent effect Confidence limits
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TABLE 2 INTERPRETATION OF CANCER PREVENTION TRIALS: EXTERNAL ASPECTS
Generalizability of results Volunteers Defined populations Effectiveness versus efficacy Comparison to other studies Reporting results
study subjects, and the spectrum of cutaneous and other side effects previously reported for retinoids, albeit at substantially higher doses. Other secondary hypotheses relate to the methods used to measure compliance in the intervention groups and the effect of motivating compliance. Post hoc hypotheses, developed after the trial was initiated and often after interim analyses has occurred, must be defined and clearly stated as hypotheses generated by the trial and thus not to be conclusively answered by the trial. The assumptions used during the design of the trial should be compared with the observed data from the trial. Not only should the target number of subjects that was part of the trials design be compared with the number of subjects actually enrolled but the total number of endpoints targeted and observed should be compared. Longer follow-up commonly results in the accumulation of more endpoints for cancer prevention trials. Thus, extending the duration of follow-up and accumulating added endpoints may address discrepancies in the targeted number of endpoints anticipated and the actual number needed. The common observation that volunteers for disease prevention trials have lower morbidity and mortality than the general population (i.e., health volunteer effect) may result in longer follow-up to obtain the targeted number of endpoints. For example, the 3% annual decline in cardiovascular mortality for the U.S. population observed during the conduct of the Multiple Risk Factor Intervention Trial (MRFIT) resulted in fewer endpoints than expected in the control group and reduced power to evaluate the primary hypothesis (1). Increased follow-up could have addressed that anticipated issue. Subject drop-in and drop-out can have a significant impact on the sample size actually required for a cancer prevention trial. While it is recommended that drop-in and drop-out be considered in the sample size calculation, differences between the assumed and observed frequency of subjects that drop-in or drop-out of the trial must be considered with corresponding changes in sample size during the conduct of the trial. Methods have been published that demonstrate the impact of compliance on statistical power and the recalculation of sample size (2, 3). Strategies to recruit study subjects should be clearly defined, including how potentially eligible people are informed of the trial, as well as the entry and exclusion criteria. Strategies may change from the time the trial is designed and are subject to change throughout the conduct of the trial. For example, recruitment for the SKICAP trials was planned to be exclusively through dermatologists in the Tucson metropolitan area. This plan was effective during the first year of recruitment. More recently decreased enrollment has resulted in the use of other
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strategies, including the use of the print, TV, and radio media to inform potentially eligible subjects of the trial and the need for additional volunteer participants. Also, enrollment was expanded from one to four different communities. Many prevention trials recruit free-living individuals who have minimal or no ongoing clinical care. Thus strategies such as those used in the SKICAP trials that are cost effective and directly inform potential subjects need further development and evaluation of their impact on the generalizability of the trial. Our experience to date indicates that approximately 50% of all persons who show interest in participating were scheduled for screening at one of the enrolling clinics, approximately 25% of all persons met entry criteria and were accrued into the run-in period, with 75-80% of those accrued going on to be enrolled and randomly assigned to one of the intervention groups. Thus, approximately 20% of all persons who show an interest in participating in the SKICAP trials meet the defined recruitment criterion and are enrolled. This percentage appears to be higher than that reported for other disease prevention trials. The definition of the intervention should include its type, dose, and dose rate. Changes in any part of the intervention that occur during the course of trial require complete description. In designing the SKICAP trial for AK subjects, isotretinoin was the retinoid originally planned as the experimental agent. However, shortly after beginning subject accrual, the pharmaceutical supplier chose to withdraw the availability of isotretinoin from the SKICAP trial. Retinol and retinol placebo were substituted after documentation of adequate rationale. Fortunately the change in the experimental agent occurred when all subjects were on the placebo run-in phase and no subject had been randomly assigned to the experimental or placebo group. The resulting change in retinoid for the SKICAP trial in AK subjects did result in unavoidable confusion among some subjects and a short delay in the trial. Far more deleterious effects on the interpretation of the trial would have occurred if a change in experimental agent had occurred later in the trial. Intervention assignment and blinding require careful consideration during the trial design and after the trial is initiated. Stratification factors, including inclusion and exclusion criteria, and how they may have changed during the conduct of the trial will provide better understanding of how the trial was actually carried out. Also, the completeness of the blinding of subjects, clinic staff, and referring physicians should be evaluated. Prior to the initiation of the SKICAP trials, some of the cooperating dermatologists indicated that they might be able to determine which subjects were taking the assigned retinoid due to anticipated cutaneous side effects. The importance of maintaining subject blindness has been repeatedly emphasized to all referring dermatologists. A recent survey indicated that cutaneous side effects observed by dermatologists were not extreme enough to provide an easy indicator of which subjects were in fact taking retinoids. Thus, SKICAP dermatologists have not been blinded as they had anticipated. Another example of the success of maintaining the blind nature of the trial relates to the placebo used in the SKICAP trials. One subject reported that he had attempted unsuccessfully to determine whether he was assigned retinoid or placebo. The
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subject had requested information of his pharmacist as to the appearance and content of the capsules provided by SKICAP staff. Fortunately, the pharmacists indicated that the capsules looked in all ways like retinoid capsules. A point to be learned from these experiences that may relate to many blinded intervention trials is that an apparently well-designed plan to keep the trial double-blind can be undermined by the referring medical staff or the subjects. The degree of unblinding should be determined and reported. Compliance to the prescribed intervention is critical to the success of a disease prevention trial and is markedly complex to measure and motivate. Measurement of compliance could use a variety of subjective or objective methods. Limitations in resources, subject tolerance, and fundamentaal knowledge of human behavior have resulted in pragmatic choices regarding compliance methods used in the current generation of cancer prevention trials. To obtain an estimate of compliance for each subject participating in the SKICAP trials, three subjective methods have consistently been used. The primary measure of compliance has been the number of capsules returned by the subject at each follow-up visit. Other measures include the subjects recording on a monthly calendar form the time each day they take their capsule and the number of capsules reported as not taken during randomly selected 7-day periods. While all three methods were highly correlated and indicated that over 90% of study subjects were complying with the intervention, validation of the subject’s self-report was desired. Compliance was objectively estimated using a biologic marker (10 mg riboflavin combined with the retinoid capsules) and a computerized pill blister pack. The pill pack was developed in collaboration with Seth Eisen, M.D., from Washington University, and electronically records the time and date that each blister was opened. Each of the objective methods to measure compliance were highly correlated to the pill count method and indicated that subjects were accurately and consistently reporting their compliance to the prescribed intervention. Methods used to motivate compliance including the type, frequency, and uniformity of application require added consideration. The use of a run-in period to assess the likelihood of long-term compliance prior to random assignment of the intervention may be extremely useful in identifying a compliant cohort. Even though such run-in periods may be carefully carried out prior to random allocation, the proportion of subjects that drop-out or drop-in to a trial after random assignment will have substantial reduction on the power. Thus, to ensure an adequate interpretation of the trial by ensuring adequate power, the number of endpoints may require to be changed (commonly increased) prior to terminating a trial. A change in the number of endpoints can be commonly accomplished by increasing the total sample size or extending trial follow-up. In addition to reports of compliance by the subject, other markers of compliance have been investigated, including subject characteristics such as demographic, social, economic, and behavioral factors, and frequency and degree of side effects. The interrelationship between subject characteristic and compliance to date has not provided a well-defined motivational plan that directly results in high compliance among all or nearly all subjects. While further compliance re-
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search is needed, cost considerations and potential dilution of the ability to answer the primary hypothesis need to be balanced. A valid estimate of subject compliance may be minimally essential to the interpretation of a trial. Improved understanding of the relationship between compliance and safety during a cancer prevention trial may result from an inadequate interpretation of the data. The spectrum of side effects known or anticipated prior to the start of a trial should be monitored and updated during the conduct of the trial. How safe was the experimental intervention? Was the blind nature of the trial affected? These are two key questions that influence the interpretation of a trial. The plan to use retinoids in the SKICAP trials resulted in an extensive clinical and pathological monitoring of subjects with ongoing review by two extramural safety monitoring committees. The continuation of the trials indicates that side effects have not been different than anticipated and adequately tolerated using the modest dose of retinoids. How endpoints were defined, measured, and verified during the actual conduct of the trial will have an impact on study interpretation. The requirement for pathologically confirmed diagnosis of invasive cancer is commonly used for most of the ongoing cancer chemoprevention trials. Next generation cancer prevention trials may successfully utilize biochemical or other intermediate endpoints. The biologically valid relationship between the intermediate endpoint and the cancer endpoint will clearly have an impact on the interpretation of such intermediate endpoints and thus the effectiveness of the intervention. One of the potential interpretations derived from the current generation of cancer chemoprevention trials is the potential to identify and begin to validate such a relationship. Risk factors that are putatively related to study endpoints again are commonly well defined during the design phase and measuredduring the conduct of the trial. An adequate interpretation of the trial would include the actual magnitude of the risk factor. This should not only include confounding factors such as age or gender but also event modifiers which have differing magnitudes of effect on different subsets of the study population. One example of such event modifiers is an assessmentof dietary intake of key micro- and macronutrients. It may not be adequate to simply consider such dietary factors as simple confounders, but a careful assessmentof their role as an event modolier should be included in the interepretation of the trial. Follow-up may be classified as one of the most important aspects of a cancer prevention trial. Without sulficient follow-up, there will be inadequate numbers of endpoints and insufficient power to evaluate the hypotheses. Frequency of followup should be considered, particularly whether follow-up procedures were equally applied to both the experimental and control groups. A key question is whether the duration of follow-up has been sufficient to adequately discriminate between two markedly different interpretations of the study: first, the situation in which the experimental intervention did not markedly reduce the risk of cancer and second, the experimental intervention was not fully efftcacious for some latent period. For example, the benefits of stop smoking might be interpreted as ineffective in lowering the risk of lung cancer in heavy smokers if the duration of follow-up was not less than 2 years. A decrease in risk begins to appear after 2
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years with a follow-up duration of 9 years required before maximal decrease is observed (4). Analyses
Analysis of the data from a cancer prevention trial is a critical part of the complete interpretation of the trial. There may be differing and possibly competing analysis procedures that might be carried out. A key question as to whether different analyses yield different results must be carefully considered in the interpretation. The intention to treat philosophy suggests that all patients once randomized should be analyzed. An alternate method of analysis would be to include only a subset of “evaluable” subjects in the analysis. Such a subset might be defined by considering a certain dose level or compliance required in order for a subject to be included in the analysis. Critical comments have been appropriately expressed regarding such subset analyses (5). Interpretation of the data will benefit from a careful separation between the methods used to evaluate the primary hypotheses and statistical methods used to evaluate secondary or tertiary hypotheses which may be more effectively addressed in subsequent trials, A multitude of statistical methods are available for the analysis and comparison of intervention groups. Statistical methods deserving consideration include first, those using the frequency of events at a particular time point after the trial has begun (e.g., 5 years); second, the use of the proportional hazards model to address both the occurrence and the duration of time until endpoints occur, and third, use of relative risk methods recently proposed by Prentice (6). Each of the methods noted can accommodateadjustment for multiple risk factors. Of particular interest and somewhat more characteristic of cancer prevention trials is the occurrence of multiple endpoints for an individual subject. For example, in cancers of the skin, colon, or cervix it is possible and often likely that not one but multiple tumors or precancerous lesions may be diagnosed. In addition, the use of biochemical or other intermediate tumor markers may include a natural history of progression followed by regression and subsequently followed by progression. The occurrence of multiple endpoints provides new opportunities to include this additional information in the analysis in hopes of providing a better interpretation of trial data. The validity of the analysis and corresponding interpretation of the trial may be affected by which risk factors one considers in the analysis, including both causal as well as preventive factors. For example, the dose of a carcinogen such as ultraviolet light for skin cancer would be included in the multivariate analysis for the SKICAP trials. Of possible equal importance is the inclusion of preventive factors such as dietary nutrients other than vitamin A that should be considered. A key to this consideration and the validity of the analysis is how these causal and preventive factors are included in the analysis and whether they should be considered as risk modifiers (interaction terms) in the multivariate analysis. At this present state of the conduct and analysis of cancer prevention trials, it is difXcult at best to determine which, if any, and in what form such preventive factors should be included in the planned analysis of the data. It may be more appropriate to consider this a secondary analysis and include different mathematical func-
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tional forms of the causal and preventive factors in the analysis. Such an approach may lead to different results and require careful interpretation and reporting of trial data. The distribution of subject characteristics at the time they enter a trial may change during the enrollment period. This is of interest especially in a prevention trial because of the large number of subjects commonly required and the likelihood of enrollment lasting for several years. It would be of interest to analyze the change over time of the distribution of entry characteristics and the distribution of endpoints. During the first few months of a cancer prevention trial subjects may be recruited from an existing prevalent pool of eligible subjects; however, continued subject recruitment may come from subjects who have recently achieved the eligibility criteria. For example, in the SKICAP-BCC/SCC trial, there was an identified prevalent pool of persons that met eligibility criteria at the time the protocol was designed, approximately 2 years before the trial was actually initiated. Many of the people had a history of more than eight skin cancers. Consenting subjects from the prevalent pool were enrolled in the SKICAP trial during the first 12 months of enrollment. After which subjects were enrolled as they were diagnosed with the minimal number of requisite skin cancers to meet eligibility criteria. Thus, the time to the occurrence of their next skin cancer may differ as to the carcinogenesis stage as reflected by their skin cancer history. Delay in the preventive action or latent effect of the experimental intervention requires careful evaluation during the analysis of a cancer prevention trial. The impact of a latent effect, the resulting reduction in statistical power, and the corresponding requirement for an increase in the number of endpoints has been reported previously (2). While yet undetermined, it appears reasonable and prudent to assume that an extended period of carcinogenic exposure such as sunlight exposure may not be immediately reversed by an experimental chemoprevention or other intervention. Considering that subjects participating in a cancer prevention trial do not and often cannot totally eliminate their carcinogenic exposure it may be appropriate to assume that a cancer preventive agent will not demonstrate its full effect before 2 or 3 years of participation on the trial. A cancer prevention trial planned for a 3-year median follow-up of all study subjects may be severely limited in its ability to adequately answer the null hypothesis if the latent period is at least 1 year in duration. A careful analysis of a trial would not only estimate compliance of subjects participating in each of the intervention groups but also the presence and duration of a latent effect. As both of these issues can substantially reduce the statistical power of the trial, adjustment of sample size or study duration should be carried out prior to the termination of the trial. Confidence Limits
Use of confidence limits has been suggested by numerous authors as a method to improve the interpretation of a trial (7). Added emphasis appears to be appropriate for use of confidence limits to estimate the range of cancer risk reduction due to the experimental intervention that is consistent with the data. The requisite number of endpoints should be adequate to yield the indicated statistical power planned during the design of the trial. The maximum and minimum effect of the
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experimental intervention obtained from a confidence interval may improve the interpretation of a prevention trial. EXTERNALASPECTS External aspects of the interpretation of a prevention trial include the generalizability of the results of the trial, consideration of the efficacy of the intervention, comparison of trial results to other studies, and the reporting of the results of the trial. External aspects should receive added emphasis for cancer prevention trials due to the small number of Phase III-V trials to be carried out for specific types of cancer or interventions. Generalizability of Results Generalizability is the one aspect that most authors are reluctant to fully discuss but the one area that most readers of the published report of a trial are eager to interpret. Because the investigator is in the best position to know the advantages and limitations of the prevention trial, adequate interpretation including its generalizability should be provided. However, limitations do exist in the ability of the investigator to generalize the results of the trial. For example, generalizing the results of a trial with high risk subjects is difficult at this early stage of cancer prevention research. It is unclear if such a generalization is appropriate or what limitations may apply. One aspect of the generalizability of a prevention trial is how the subjects relate to a defined population. Subjects participating in a trial or any type of research are volunteers and may not be a randomly selected sample from a defined population. The reference frame for the study subjects may have been a geographic area, occupational group, or a medical clinic. For example, SKICAP participants include volunteers from the Tucson and Phoenix metropolitan areas. In contrast participants from an enrolling clinic in San Diego, California, are volunteers from one specific dermatologic clinic. Interpretation and generalizability of a prevention trial may be improved if the participants are compared with a defined population. Use of a population-based cancer registry may provide one available comparison group. Comparison of the registry population with subjects from the placebo (control) group that are diagnosed with cancer during the trial would indicate the similarity between the two groups for available risk factors. Unfortunately, it is not common for cancer risk factors to be abstracted as part of a cancer registry. Another alternative for comparison may be persons selected as controls for a population-based cancer etiology case-control study or as population-based subjects selected for participation in a cohort study. The recent initiation of a pair of skin cancer case-control studies in Southeastern Arizona that include a randomly selected populationbased control group is one example of a representative sample from a defined population that will be used for comparison with the ongoing SKICAP trials. The extensive risk factor information collected from the control group will be used for comparison with the distribution of factors for SKICAP participants. Such a procedure will not only provide a comparison of risk factors for the cancer type of primary interest but also provide some indication of the possible magnitude of a healthy volunteer effect that is commonly seen in many medical research trials.
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vs Efficacy
Efficacy is commonly defined as the effect of an intervention if total compliance to the prescribed protocol was achieved by all participants. Most prevention trials are not able to measure efficacy directly as participant compliance is often less than complete. Effectiveness of an intervention is the often achievable measure of effect that is influenced by the level of compliance each participant actually achieves during a trial. Although the comparison of efficacy between experimental and control interventions is the goal of a cancer prevention trial, the often achievable measure is the comparison of the difference between the effectiveness of the interventions. Though not often able to be measured directly, the difference in efficacy may be estimated if the level of compliance can be separately quantified for each of the intervention groups. An estimate of intervention efftcacy may be obtained, using one of several published methods (8,9) and the study-derived estimates of intervention effectiveness and compliance. Such a measure may provide improved interpretation and ability to compare with similar measures from other prevention trials. Comparison
to Other Studies
The impact of a specific cancer prevention trial on the control of cancer in a general population is, at best, difficult to determine. The example of the changing dietary, exercise, and smoking behavior of the U.S. population may not be easily related to one or even a group of trials. It is more likely the composite of research, including descriptive, analytic, and experimental epidemiology studies, plus professional recommendations and the individual’s judgment to adopt the recommended intervention. The generalizability of an individual cancer prevention trial and its integration into the composite of prevention strategies may be assisted by the use of metaanalysis. Extensively used for a number of years by social scientists, the use of metaanalysis in public health to obtain an integrated interpretation of a collection of research papers is becoming acceptable (10). Long-term follow-up of the participants in a prevention trial may not only provide an adequate number of endpoints to answer the primary hypothesis but important additional information that could be valuable for improved interpretation and comparison between numerous prevention trials. For example, long-term behavioral changes in the participants to adapt the prescribed intervention plus information on the type, severity, and frequency of side effects can provide important new information for the planning of community intervention trials. For example, the Phase III SKICAP trials might be extended in follow-up and be redefined as a Phase II methodology trial evaluating the above-noted issues of compliance and safety as well as providing commonly unavailable information regarding diffusion of research findings throughout a community. Reporting
Results
An integral component of the interpretation of a prevention trial like all research studies is a careful reporting of the results of the trial. The investigator is truly in the best position to know the strength and weakness of the trial and should have
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the obligation to report these plus the discussion of the generalizability of the trial results. The publication of trial results and their interpretation provides one’s peers with the opportunity to evaluate and integrate the findings into the next generation of prevention trials. Such reporting also provides the necessary scientific foundation on which to develop the community recommendations and their relative cost effectiveness for disease prevention. REFERENCES 1. Multiple Risk Factor Intervention Trial Research Group. Multiple risk factor intervention trial: Risk factor changes and morbidity results. JAMA 1982; 248:1465-1474. 2. Moon TE. Clinical trials of cancer prevention agents: True versus observed prevention effects. Sfat Med 1986; 5435-439. 3. Donner A. Approaches to sample size estimation in the design of clinical trials-A review. Star Med 1984; 3:199-214. 4. Doll R, Peto R. Cigarette smoking and bronchial carcinoma: Dose and time relationship amongst regular smokers and lifetime non-smokers. .I Epidemiol Commun Health 1978; 32:303. 5. Byar D, Simon RM, Friedewald WT, et al. Randomized clinical trials: Perspective of some recent ideas. N Engl .I Med 1976; 295:74-80. 6. Prentice R, Mason MW. On the application of linear relative risk models. Biometrics 1986; 42~109-120. 7. Rothman K. Modem Epidemiology. Boston: Little, Brown, 1986:119-350. 8. Lachin JM. Introduction to sample size determination and power analysis for clinical trials. Controlled Clin Trials 1981; 2:93-l 14. 9. Wu M, Fisher M, DeMets D. Sample sizes for long-term medical trial with time-dependent dropout and event rates. Controlled Clin Trials 1980; 1:109-121. 10. Louis TA. Findings for public health from meta-analysis. Annu Rev Public Health 1985; 61-20.