Management of localized prostate cancer: An epidemiological perspective

Clinical Oncology(1995) 7:151-159 © 1995 The Royal Collegeof Radiologists

Clinical Oncology

Review Article Management of Localized Prostate Cancer: An Epidemiological Perspective R. H. Harwood Department of Public Health, Royal Free Hospital, London, UK

INTRODUCTION

Some doctors, notably epidemiologists, have been questioning the value of screening and curative treatment for localised prostate cancer. This movement has been based largely on misleading studies and has left the general public with the impression that deferred treatment is as effective as active therapy for all men with clinically localised prostate cancer. Since there is no cure for advanced disease, the only way of reducing the morbidity and mortality from prostate cancer is to detect it earlier and treat it at a curable stage [1]. The debate on the management of localized prostate cancer has been described as a 'sort of yelling debate' [2]. The literature contains many more reviews and expert commentaries than it does papers presenting original data [3]. Many depend on the logic encapsulated in the final sentence of the quotation above. However, the test of this logic is whether it works in practice. Many clinicians, especially in the United States, understate the uncertainties inherent in interpreting research evidence, and may hold unduly optimistic opinions of the value of interventions. Conversely, public health commentators may appear nihilistic in their attitude towards treatment of a disease that carries appreciable morbidity and mortality. Epidemiology is the quantitative study of the occurrence, distribution, risk factors for, and control of, diseases in populations [4]. It attempts to describe causal associations between exposures (e.g. treatments) and outcomes (e.g. cancer mortality). It also serves to inform health policy. Thus we wish to know both whether an association exists and how large an effect is seen. Clinical epidemiology is a branch in which the findings of epidemiology are applied at the bedside; it is the basis of what has become known as 'evidence-based medicine' [5]. I aim briefly to review the different types of epidemiological evidence, and to illustrate their application and limitations in evaluating treatments for localized prostate cancer. Coverage of studies will therefore be selective rather than comprehensive.

Correspondence and offprint requests to: Dr R. H. Harwood, MRC Health Services Research Fellow, Department of Public Health, Royal Free Hospital, London NW3 2PF, UK.

OBJECTIVES OF MANAGEMENT It is undeniable that prostate cancer is a problem. In the UK, it is the certified cause of 3.2% of all male deaths [6], each death representing an average 9 years of life lost [7]. It also causes morbidity, either locally (with urinary outflow obstruction) or systemically (painful metastases and general debility). One objective of intervention might be to cure the cancer. Experience shows that patients are often willing to tolerate considerable adverse effects of treatment if there is a reasonable probability of being cured of a potentially fatal disease. Even if the disease is not curable, prolongation of life may be the goal. This is particularly relevant since prostate cancer incidence increases exponentially with age. Many men will die before their cancer has caused major problems, socalled 'competing mortality'. Thus, a commonly used outcome measure for treatment is cancer-specific mortality. This is a reasonable intermediate indicator of whether a treatment looks promising. However, the real goal of intervention is a reduction in all-cause mortality. This was well illustrated in prostate cancer epidemiology by the results of a Veterans' Administration Co-operative Urological Research Group (VACURG) trial in metastatic cancer [8]. High dose oestrogens decreased cancer-specific mortality, and lengthened time to progression, but the all-cause mortality was unchanged because of an increase in cardiovascular mortality. Prolonging life is itself only a partial objective in cancer care. Quality of life is increasingly recognized to be of comparable importance [9], especially with elderly subjects. Quality of life may be affected by both disease and iatrogenic processes. In many patients, improvements in quality of life will parallel improvements in survival, but this is not necessarily so. Radical treatment of prostate cancer may result in major moribidity (incontinence, impotence, urethral stricture and bowel injury) [3,10] as may palliative hormonal treatment (impotence, hot flushes, weakness and loss of vigour, osteoporosis). However, the median length of remission after the hormonal treatment of metastases is 12-18 months, and median survival is 2.5 years. Measures that retard progression to metastatic disease are therefore also valuable, although formal determination of a range of quality of life indicators should be undertaken in trials.

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EPIDEMIOLOGICAL EVIDENCE Three basic types of epidemiological evidence contribute to the evaluation of prostate cancer treatments: the case series, ecological study and the randomized controlled trial [4,11]. Two further techniques have been used and require comment: meta-analysis and decision analysis. Cohort studies in this context are similar to case series. Case-control methods have not been used, although there has been interest in their application in health services research; a recent example used the technique to evaluate prostate cancer screening [12]. All these methods aim to establish the presence of associations between 'exposures' (in this case type of treatment) and 'outcomes' (cure, all-cause mortality, cancerspecific mortality, progression-free survival, complications). In general, observed epidemiological associations can have any of four explanations [13]. They can occur by chance (a possibility quantified by the P-value), because of bias, because of confounding, or because the relationship is causal. Bias occurs when there has been some (unintentional) error or distortion in the collection of data, which results in invalid comparisons being made. Confounding occurs when there is a real relationship, which is due to some alternative explanation, a third factor that is associated with both the exposure and outcome (such as the age or tumour grade distribution of patients receiving different treatments). The confidence with which one can assume a relationship is causal varies according to the type of evidence, because of the different biases to which they are prone and the ways in which they overcome the problem of confounding.

Case Series The case series comprises a description of the clinical course of a group of patients undergoing a particular treatment. Unless the disease has a fairly uniform and rapidly developing outcome if untreated (such as pneumococcal pneumonia), data such as this is of limited use. However, this is the commonest type of evidence in the evaluation of treatment for prostate cancer. I will consider some illustrative examples. Belt and Schr6der studied 464 patients who had radical prostatectomies between 1928 and 1970. The age range was 46--86 years (mean 65). One hundred and forty-four patients were noted to have local turnout extension at operation. Survival over 20 years was documented. All-cause survival was 69% at 5 years, 44% at 10 years, 22% at 15 years and 15% at 20 years. Twenty-five per cent of patients died of cancer. Ten- and 15-year survival rates were 55% and 31% for patients with pathologically localized tumours (12% died of cancer), but only 37% and 17% for those with local extension (33% died of cancer) [14]. Patients with localized tumours fared not much worse than was expected from their 'survival probability' based on age- and period-matched mortality rates for the general population. Walsh and Jewett reported similar 15-year survival amongst 57 of 70 patients with clinical Stage B1 disease, who were operated on between 1951 and 1963; 54 had

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pathologically localized disease, and 51% were alive and disease-free 15 years later. Of those who had died, 17% had recurrent cancer and 32% died apparently disease-free. This was the same 15-year surival as for the general population of the USA in 1950 [15]. The main problem with case series is lack of a comparison or control group. Life tables for the general population are not suitable for this purpose. The general population contains people in all states of health, wealth and background. The surgical series is a highly selected group of fit men with the resources to undergo major surgery at an internationally renowned institution. We are told that a later series from Walsh [16] contained patients 'from 47 of the 50 states in the United States'. Follow-up on Belt and Schr6der's series was almost complete, but we know nothing of the fate of the 13 patients who Walsh and Jewett could not trace. In general, such patients have worse health outcomes than those who are found, and they cannot be assumed to be a random sample of the eligible population. Surgeons generally do not wish to perform futile surgery, and will select, consciously or unconsciously, patients with the best prognosis. We do not know whether the operation saved the patient, or if there was fortuitous selection of patients who would have survived anyway. Moreover, any historical series raises the question of technical advances and the relevance to patients today of data obtained on those operated on so long ago. Comparisons need to be between contemporaneous groups. If such observations appear oversceptical, they simply reflect sources of uncertainty, which prevent the drawing of firm conclusions when assessing the efficacy of interventions. Similar problems affect series of patients treated by radiotherapy. Bagshaw et al. described 1119 patients with Stage A (To), B (T1_2) or C (T3_4) cancer treated between 1956 and 1990. Ten- and 15year disease-specific survivals were 84% and 84% for men with To tumours, 77% and 65% for men with T~ tumours, 64% and 42% for men with T 2 tumours, 50% and 30% for men with T3 tumours, and 25% and 25% for men with T4 tumours. All-cause survivals at 10 and 15 years were 72% and 42% (To), 60% and 40% (TO, 52% and 30% (T2), 35% and 17% (T3), and 15% and 15% (T4) [17]. Fewer patients were free of disease than reported for surgery, but, using Bagshaw's assessment of who would have been a surgical candidate in his series, the difference was small (51% versus 46%). We still cannot say whether this comparison is a reasonable one, or whether unknown biasing or confounding factors distort it. If there is a difference, we cannot say whether the intervention made the difference; the patients were different and had different disease. For instance, less fit men, men with higher grade disease, or large tumour volumes, may be referred for radiotherapy as opposed to surgery. However, the survival curve for the 96 men with impalpable To disease showed considerably better survival over 10 years than the expected survival for the general population, suggesting that they were either younger or fitter than the population with which they were being compared. We also do not know what would have happened if nothing had been done. Bagshaw reports patients alive at 20 and 25 years, despite initial

Management of LocalizedProstate Cancer tumours that were locally very extensive, including some patients with T 3 tumours, who were apparently disease-free at 25 years, which suggests cure, misdiagnosis, misstaging, or very benign disease indeed. The problem in both these cases is that we do not know enough about the denominator population, the group of people from whom cases were selected. Natural history studies are the non-intervention equivalent of the case-series. In the best of these, the denominator is known when a population-based register is used. These include all cases reaching medical attention in a defined population in a specific time period. Johansson et al. followed up 98% of a series of 227 patients to reveal 5- and 10-year allcause survivals of 72% and 44%, and disease-specific survivals of 94% and 87%. Progression-free survival was 72% at 5 years and 53% at 10 years, but prognosis was much worse in high grade tumours [18,19]. A meta-analysis of observational studies has been performed [20], and is discussed below. Further discussion of possible biases in case series data is included when considering the comparisons made between the different treatment strategies.

Ecological Studies In this type of study the unit of investigation is a population (or other grouping) rather than the individuals within it. An example relating to prostate cancer has recently been published by Lu-Yao and Greenberg, and is worth reviewing in some detail [211. Aetiological epidemiology considers ecological studies to provide a quick but preliminary form of evidence. The observed strength of association is often attenuated by lack of validity in the exposure and disease incidence data. Proxy measures are often used. For example, a study of the aetiology of prostate cancer may compare national average meat or dairy product sales with prostate cancer mortality from death certificates. The variable of real interest may be saturated fat consumption, and death certificates are notoriously inaccurate [22], possibly in a systematic way if there are national differences in certification 'habits'. Control of confounding is usually impossible. In evaluating treatment, however, these criticisms do not necessarily apply. There is little doubt about what the relevant 'exposures' are: radical surgery, radiotherapy, and immediate or delayed hormonal manipulation. Moreover, population-based cancer registries provide reasonable surveillance data. Lu-Yao and Greenberg examined data from nine such registries in the USA, covering about 10% of the total population between 1983 and 1989. Registry data included stage and treatment within 4 months of diagnosis. Age-specific mortality rates for prostate cancer were available for 1983-1988. Analyses were restricted to white men aged 50-79. Age-adjusted prostate cancer incidence increased from 276 per 100 000 in 1983 to 383 per 100 000 million in 1989, an increase of 6.4% per year. Two-thirds of the increase was in localized disease; the remainder was in regional disease, probably accounted for by up-

153 staging of surgically treated patients. There was no change in the number of new patients diagnosed with metastases already present (i.e. there was no 'stage shift' towards more localized stages). The incidence of prostate cancer in 1989 varied amongst the nine areas from 268 per 100 000 to 607 per 100 000. Despite this, mortality from prostate cancer was almost identical across the areas, and did not change between 1983 and 1988. Over the study period the average rate of radical prostatectomy increased from 25 per 100 000 in 1983 to 98 per 100 000 in 1989, when the operation rate per 100 000 across the nine areas varied between 43 and 224. The proportion of patients receiving radiotherapy remained constant. The most likely explanation for the differences in incidence was the detection of occult disease (rather than true variation in incidence). The ecological analysis of treatment efficacy showed no relationship between prostate cancer mortality and the proportion of cases operated, suggesting that curative surgery is ineffective. A long lag between the widespread use of curative surgery and decreased mortality would be expected [1], although the variation in radical prostatectomy rates must have predated the study period considered. Mortality rates were averaged over a 5-years period, during which the intervention was being applied increasingly widely. There was also scope for ascertainment bias in the assignment of cause of death. In the areas with the high incidence and operation rates, awareness of the disease may have led to its over-representation on death certificates.

Randomized Controlled Trials History has demonstrated that the only way to avoid the distorting effects of bias and confounding, due to known and unknown factors, is to allocate treatments at random. Even then, unless the size of the trial is very large, there is no guarantee that the different treatment arms will be balanced for all potentially important factors (age, grade, stage, biological potential, operator skill, comorbidity and so on). The avoidance of bias and confounding is the reason for the slightly counter-intuitive requirement that outcomes be evaluated according to initially assigned treatment group ('intention-to-treat') rather than the treatment actually received. For example, consider a trial in which patients with clinically localized (To-2, Nx, M0) prostate cancer are randomized to radical prostatectomy, radical radiotherapy or hormonal therapy delayed until symptoms arise. Thirty per cent of the surgical group are up-staged (because of capsular invasion or regional lymph node metastases) and are reassigned to radiation or horomonal therapy. Clearly, the surgical group has lost the subjects with the poorest prognosis. In the non-operative groups, these subjects will never be identified. If they are excluded from the analysis of survival after surgery, the comparison with the non-operative arms will be biased. If the subjects with a poor prognosis are then added to another group, the bias is exaggerated. The same holds for other less obvious (and perhaps unknown) prognostic factors. Unless patients are withdrawn equally from each group, and

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at random, which they rarely are, any exclusions from the analysis unbalances the randomization. The corollary of this is that statistical power is lost; it is more difficult to show a real difference amongst the patients with surgically staged localized disease, since they are 'diluted' by incurable patients with locally progressive or metastatic disease. The best solution to this is to make the study groups as homogeneous as possible before randomization, for example, by staging lymph node biopsy. Randomized trials of surgical interventions are difficult but not impossible [23,24]. The V A C U R G studies pioneered the application of randomized evaluation techniques in surgery [25], but 30 years have passed since they were initiated. There have been only five randomized trials of therapy for localized prostate cancer: radical surgery with or without adjuvant high dose oestrogen; radical surgery versus delayed hormonal therapy; non-surgical candidates randomized between immediate and delayed hormonal therapy; radical surgery versus radiotherapy; and orchidectomy versus radiotherapy or both. More trials are in progress or planned, including trials of: immediate versus delayed orchidectomy [26]; radiotherapy with or without a gonadotrophin releasing hormone agonist [27]; and trials comparing surgery, radiotherapy and medical management [19,27,28]. The first V A C U R G study from 1960 to 1967 randomized 120 patients with incidentally found impalpable disease ('Stage I'), and 179 with palpable disease confined to the gland ('Stage II'), between prostatectomy plus placebo or prostatectomy plus diethylstilboestrol 5 rag/day. The main finding from this (and the better known part of the study comparing hormonal treatments in disseminated disease) was that high dose oestrogens are associated with a high cardiovascular mortality. The all-cause survival for Stage I oestrogen-treated patients was worse than for those treated with placebo, whilst the survival curves for Stage II disease were indistinguishable [8,29]. From 1967 to 1975 the same group randomized 76 'Stage I' patients and 66 'Stage II' patients between radical prostatectomy plus oral placebo or oral placebo alone [30]. Patients were staged by rectal examination findings, radiological skeletal survey, and serum acid phosphatase determinations. After up to 9 years of follow-up (median 7 years) there were 43 deaths from all causes amongst 111 evaluable patients (i.e. 22% of patients were excluded for various reasons). Survival in the operated group was 62% compared with 60% in the non-operated group for both stages combined (difference 2%; 95% CI +20 to -16). Differences in proportions surviving were 12% in favour of operation in Stage I (95% CI - 1 2 to +36), and 13% in favour of non-operation in Stage II (95% CI - 1 4 to +40). Sixteen patients showed disease progression (11% prostatectomy; 18% conservative; 95% CI for difference +20 to - 6 % ) . Graversen et al. reported similar results at a 15-year follow-up [31]. Clearly, the main problem with this trial was lack of statistical power. The all-cause survival advantage for prostatetcomy could have been as much as 20% after 7 years. Although the investigators stated that

R.H. Harwood

an 'intention-to-treat' analysis gave identical results, the loss of so many patients from the analysis may have biased the randomization. In fact, the Stage I prostatectomy patients were younger than the nonoperated patients, which in part explains their better survival. Finally, the relatively crude staging means that any effect of aggressive treatment may have been obscured by patients who had occult metastases at diagnosis. This will have caused loss of statistical power, but will not have introduced bias. Despite these caveats, this trial must be taken seriously and counted amongst the evidence in favour of conservative management. The final V A C U R G trial in localized disease was undertaken on 148 patients who would have been candidates for radical prostatectomy but who were 'too old, too ill or refused an operation' [32]. They were randomized between placebo, diethylstilboestrol 5 rag/day, orchidectomy or both. After up to 8 years of follow-up (median 5) 72 patients had died, although none had died of prostate cancer. There were no statistically significant differences in survival between the four groups. Seven per cent of patients showed evidence of progressive disease. A nonrandomized comparison was made with patients in the first radical prostatectomy trial described above [8,29]. Age-adjusted (all-cause) survival was better in the operated patients, but the difference was no greater than that which might have occurred by chance alone, and, of course, the general health of the surgical candidates will have been better. Progression to metastases was actually higher (16%) in the operated patients, possibly reflecting their longer survival. The Uro-Oncology Research Group randomized 106 patients with localized prostate cancer (T1_2, No, M0, Stages Az-B) between radical surgery (n=47) or radiotherapy (n=59) [33]. Staging was thorough and included bone scintigraphy, serum prostatic acid phosphatase and staging lymphadenectomy. The trial end-point was the 'first evidence of treatment failure' (distant metastases or persistently elevated acid phosphatase). Four patients randomized to radical surgery requested radiotherapy and three patients randomized to radiotherapy requested surgery, these were analysed according to the treatment they actually received. Two patients were excluded from the surgery group, as they received radiotherapy in addition for node-positive disease and local recurrence. Other exclusions were for non-cancer death (radiation two, surgery one), refusal (one in each group), 'misstaging' (one radiotherapy patient had the cancer diagnosis withdrawn, one surgery patient had elevated acid phosphatase). Analysis was therefore not by intention-to-treat. The KaplanMeier survival analysis presented indicated that, by 48 months, the chance of failure after surgery was 15%; after radiotherapy it was 40%, a difference that was statistically significant. The authors stated that the stage and grade distribution was the same between the two treatment arms, but the exclusions and cross-overs almost certainly biased this analysis, especially as three of the excluded patients had reached end-points. As far as one can reconstruct an intention-to-treat analysis from the data provided, assuming that no failures occurred in the cross-over

Management of Localized Prostate Cancer

patients, and restoring the three excluded surgical patients with progressive disease, the crude proportions of failures were 15% surgery, 29% radiotherapy (difference 14%; 95% CI for difference - 3 to +31; P=0.10). One further problem with this study concerns the randomization. This was stated to be in balanced groups of four within each institution. The original distribution (47 versus 59) is thus highly unlikely, and suggests that some non-random selection was occurring. This trial should be treated with extreme caution or disregarded. The final completed trial randomized 277 patients to immediate bilateral orchidectomy (n=90), radiotherapy (n=88) or both (n=99). Staging included bone scintigraphy, serum acid phosphatase determination and chest radiography, but not lymph node biopsy. After 7 years, all-cause mortality and local progression requiring intervention was 10% higher in the group who received radiotherapy alone compared with the other two groups, although the differences were not statistically significant. The incidence of distant metastases was significantly greater in the group receiving radiotherapy alone, being about 20% higher at 5 years. There was little difference between orchidectomy alone and the combination of orchidectomy and radiotherapy. As in other trials, patients who progressed after radiotherapy alone were given hormonal therapy, which may have obscured any survival difference attributable to the individual therapies. Again, lack of statistical power to show real differences was a problem. The proportions dying during the trial were 76% for the radiotherapy alone group and 65% for the orchidectomy groups, with or without radiotherapy (95% CI for difference - 1 to +23). Unfortunately, we are unable to assess the possible adverse effects of immediate androgen deprivation, as no quality of life data were reported.

Meta-analysis Rarely does a single clinical trial provide overwhelming evidence about a treatment comparison. Often the numbers in individual studies are small, and the estimate of the size of the benefit of one treatment compared with another is imprecise. It is often questionable whether results from a trial in one particular setting are applicable elsewhere. Combining different trial results quantitatively (recta-analysis) allows greater power to detect small effects, more precision in estimating the size of the effect and wider applicability [34]. Four main issues arise in conducting a meta-analysis. These are: indentifying the relevant studies; selecting those of sufficient quality to include; choosing a statistic to express common outcomes; and deciding on a means of weighting the different studies to take account of their varying sizes. The validity of the results of a recta-analysis depend crucially on the quality of the studies on which it is based. For this reason, most have concentrated on randomized controlled trials. The few trials of therapy in localized prostate cancer have addressed hypotheses that are too diverse to combine meaningfully. However, data from observational studies can also be combined using recta-analysis,

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subject to the usual caveat that bias and confounding distorting the input data will result in biased results of a recta-analysis Indeed, one attempt at a metaanalysis [3] performed no quantitative analyses, since the authors considered that studies in the literature contained insufficient data to allow control for confounding variables. Chodak et al. [35] selected six of ten studies published since 1985, with 828 patients who had been managed conservatively (using hormonal therapy at the onset of symptoms). They pooled individual patient data to minimize bias [36]; they could not obtain individual patient data on the remaining four studies. Account was taken of age, histological grade, stage, country of origin and racial background. Well differentiated and moderately differentiated tumours were associated with diseasespecific survivals of 87% at 10 years and 75%-80% at 15 years. Poorly differentiated tumours had a disease-specific survival of only 34% at 10 years and 25% at 15 years. Ten-year metastasis-free survival was 81%, 58% and 26% respectively for well, moderately and poorly differentiated turnouts. The possibility that less fit men had been selected into these cohorts was excluded by comparing total and noncancer mortality with that from the general populations of the countries. The authors concluded that prostate cancer is a progressive disease when managed conservatively, and that the idea of low grade disease that would never cause problems was not supported by the evidence. Half of the patients with moderately differentiated tumours will have metastases if they survive for 10 years, suggesting a potential benefit for curative therapy. However, the strongest empirical (as opposed to theoretical) argument for radical therapy is that long term results closely follow age-matched survival curves. The same appears to be true for conservative management, despite the effects of surgical selection bias. The same outcomes were used in another metaanalysis of case series of different treatment options (radical surgery, radiotherapy and conservative management), this time wholly based on published data. Studies were included of palpable, clinically localized cancer (T1_2, N×_o, Mo; Stage B) published since 1980. Mean age, proportion with poorly differentiated disease, stage, regional lymph node status, and follow-up routines, were extracted where these were available, to allow an assessment of the comparability of data. Person-years at risk were estimated from patient numbers and mean or median follow-up time. Weighted mean numbers of patients developing metastases, dying of prostate cancer and dying of other causes were calculated and converted into a rate by dividing by the person-years at risk, using patient numbers in each study as weights. The conservative management groups comprised seven reports, containing 586 patients. They had a weighted mean age of 71 years and 7% of tumours were poorly differentiated. The rate of appearance of metastases was 25.1 per 100 person-years; the rate of prostate cancer death was 16.8 per 1000 personyears, and of intercurrent death 48.8 per 1000 person-years. The weighted mean 10-year diseasespecific survival was 84%. There were 14 reports of 2395 patients who had

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undergone radical prostatectomy. The mean age was 62 years, and 17% had poorly differentiated turnouts. Four series excluded patients with regional lymph node involvement, and two excluded patients found pathologically to have locally invasive (Stage C) disease. The rate of metastases was 12.6 per 1000 person-years, that of prostate cancer death was 7.0 per 1000 person-years, and of intercurrent death 9.9 per 1000 person-years. The weighted mean diseasespecific survival at 10 years was 93%. Radiotherapy was studied in 22 reports of 2567 patients. The mean age was 66 years. Fourteen per cent had poorly differentiated disease. Five reports included only 5 patients with negative lymph nodes at a staging procedure. The distant failure rate was 29.0 per 1000 person-years, the prostate cancer death rate was 38.2 per 1000 person-years, and the intercurrent death rate was 36.2 per 1000 person-years. The 10year disease-specific survival was 62%-73%, depending on the calculation method. These results are, by turn, fascinating, tantalizing and bizarre. Intercurrent death rates increase with mean age, but the very low intercurrent death rate in the surgical group may also indicate the effects of selecting patients fit to withstand an anaesthetic and surgery. The conservatively managed tumours were less likely to be poorly differentiated, yet the rate of appearance of metastases was no greater after radiotherapy and was considerably less after surgery. Disease-specific death rates reflected the distribution of pathologial grade for conservatively managed and radiotherapy patients, but were much lower after radical prostatectomy. The data on rates of metastasis suggest that a 15-year follow-up might show an even greater advantage for radical prostatectomy. However, 10-year disease-specific survival rates were worst for radiotherapy patients (73 %), and were only 10% better after surgery (93%) than with conservative management (83%). These observations are tempered by the long list of cautions and potential biases. All the relative advantages and disadvantages of different treatments could be 'explained away' qualitatively by these effects. We cannot adjust for them statistically because we lack the data. The first to consider is the effects of surgical selection and staging. There will always be a tendency to select smaller tumours for surgery, even when all are classifiable as Stage B (a problem known as 'residual confounding') [37,38]. Moreover, several surgical series excluded patients who were up-staged at operation. Both tendencies will give an apparent advantage for radical surgery. A radiotherapy series that used surgical staging reported an 86% 10-year survival [39]. Surgical series tend to be reported by enthusiasts and experts whose results are likely to be better than those from routine practice elsewhere. It is probable that only about one-half of the conservatively managed patients received any therapy. Such patients may have lost on length of survival and progression to metastases, but gained on freedom from drug side effects. Other potential biases include different age, grade, follow-up time and surveillance for metastases (e.g. regular bone scintigraphy or clinical criteria). The summary statistics reproduced here rarely included all the reports, as each had missing data. Even the disease-specific survival esti-

R . H . Harwood

mates are suspect. Classification of cause of death may not be independent of treatment received (if, for example, radical surgery is assumed to be curative). A number of other approximations and assumptions were made, including the calculation of person-years at risk, and that the risk of dying from prostate cancer was constant with time since diagnosis (which it is not [19], and which would make the radiotherapy results look less favourable and the surgical results more so, as the latter had longer reported follow-up). A further consideration is that no data on morbidity or quality of life were available.

Decision Analysis This is a technique that helps to guide difficult decisions by combining the probability of possible outcomes with their desirability, after each of a number of different therapeutic choices [40]. An analysis of the choices facing a sexually active man aged 60-75 has been published [41]. Typical clinical assumptions were made, for example, that hormone therapy would be used if metastases developed after attempted curative procedures. A computer programme using a Markov statistical model assigned survivors of initial therapy to one of five health states. These were: no evidence of metastatic prostate cancer, metastatic cancer well controlled by hormonal therapy, metastatic cancer refractory to hormonal therapy, death from cancer, and death due to other causes. For a hypothetical population, the proportion of subjects in each state is calculated for successive 6-months periods. Rates for transition between states are derived from the literature (e.g. rate of developing metastases, rate of non-cancer death). The process is continued until the whole population is dead. The range of uncertainty can be estimated by varying rates and probabilities to observe their effects on overall outcome (so-called 'sensitivity analysis'). The efficacies of surgery and radiotherapy were assumed to be the same. Efficacy was defined in terms of the ability to forestall the appearance of metastases. Two possible levels of efficacy were assumed for each turnout grade (86%-100% for well differentiated, 30%-72% for moderately differentiated, and 5%-35% for poorly differentiated disease). The authors admitted that there was no definitive evidence in the literature to support the assumption of any benefit of any at all, but these form reasonable guesses. Operative mortality, the likelihood of treatment-related complications, and of local progression causing bladder obstruction, were also estimated. Rates of death and impotence after surgery were set at fairly optimistic levels to reflect the most skilled practice. Hormonal therapy was assumed to be 'total androgen blockade', and progression and death rates matched those in a randomized trial [42]. Non-cancer mortality was estimated from the general population (i.e. 'average' health) and separately for men from a community cohort study, who considered their health to be good or excellent. The desirability of each outcome was estimated by assigning a 'utility' value. These were based on a consensus of clinicians. The effects of

Management of LocalizedProstate Cancer 'discounting' were also considered. A year of life now is perceived as being of more value than a year of life in the future. Treatment-related morbidity is experienced now, whereas benefits are accrued in the future. Discounting takes account of this. Sensitivity analyses, with a range of utilities and discount values, were conducted. Results were presented as predicted survival after diagnosis at different ages and quality-adjusted life years for men in average or good health, following each procedure, and for each tumour grade. Differences in survival were all small, mostly under 1 year; in some patients they favoured expectant management. The greatest benefit for immediate curative treatment was for men under 70 years in 'good' health with poorly differentiated cancer, who achieved up to 1.5 quality-adjusted years' more survival under the more optimistic assumptions about treatment efficacy compared with expectant management. However, there were no benefits using the lower estimates of treatment efficacy. The two most important variables in the model were found to be assumptions about treatment efficacy and the rate of metastatic progression in untreated cases. The marginal benefit of aggressive treatment over expectant management was up to 3.5 quality-adjusted years if the most optimistic efficacy estimates, and if the highest rates of development of metastases (from the literature), are assumed. However, if the lowest reported rate of metastases is assumed, expectant management is always the best option. Varying other assumptions, such as the frequency and the utility of treatment-induced impotence and incontinence, also had the effect of changing the overall balance in favour of active treatment or expectant management. Discounting at 5% abolished the benefits of surgery or radiotherapy. Immediate treatment in men over the age of 75 was of no benefit, even for men in good health. In this model, for any given therapeutic efficacy, radiotherapy held a slight advantage over surgery due to the lower treatment-associated mortality and morbidity. However, proponents of radical surgery claim it to have greater efficacy. One striking problem with all these analyses is that, whatever else is assumed in the model, it is necessary to know precise estimates of treatment efficacy. Ultimately, the only way to judge treatment efficacy is in a randomized controlled trial. The 'lower' estimate of treatment efficacy was not the lowest estimate consistent with the data we have available. Intervention may do more harm than good (by analogy, one might ask how many surgeons would operate for small-cell lung cancer). Secondly, the results are influenced to some extent, if not greatly, by the relative desirability of the different outcome states. In reality, these estimates will vary from one patient to the next. For instance, the value of sexual potency will vary between men. Thirdly, discount rates will vary between patients. Whilst the decision analysis is interesting in its own right, and may even be useful in counselling individual patients [40], its main conclusion is that there is sufficient uncertainty to justify randomizing patients between different treatment options. Moreover, tile actual differences are likely to be small. Most of the assumptions were favourable

157 to radical therapy, and the estimates of marginal differences between types of treatment are likely to be optimistic.

Synthesis Epidemiologists recognize two types of error: rejecting the null hypothesis of no treatment effect when in reality the effects of treatment are the same (type I), and accepting the null hypothesis when one treatment really is better than another (type II). Clearly, both are undesirable. However, in the present case, the former contravenes the adage p r i m u m non nocere, breaks the implied contract with the patient who undergoes major intervention on the assumption of a reasonable expectation of benefit, and is also relatively expensive. The risk of the first type of error centres around the uncertainties in the available data, given the various types of bias and confounding to which it is prone. Risk of the second type arises because of the scepticism and nihilism engendered through assessng these problems. A few generalizations can be made. Observational data show, if anything, a small advantage for radical operative management, especially where life expectancy exceeds 10-15 years. Currently in the UK, the life expectancy of a 64-year-old man is 15 years, and that of a 72-year-old man is 10 years [6], although personal medical history will influence this for each individual. Any advantage for surgery is probably small, perhaps 10% in terms of disease-specific mortality at 10 years, equivalent to a 2%-5% difference in all-cause mortality. The difference may not exist at all, or may be larger. Any advantage will likely be very sensitive to operative mortality, the best estimate of which is 2% [10]. Two randomized trials have shown a survival disadvantage for radiotherapy compared with surgery or hormonal treatment, albeit including one of dubious validity. Radiotherapy also fares badly in observational comparisons. Why this is so is not clear, although a direct deleterious effect cannot be excluded, and various biases may explain the observational study differences. There is a suggestion that early androgen deprivation may give survival advantages over deferred treatment (from one of these trials, if the effect of radiotherapy is considered to be neutral, and if agents are used that do not increase cardiovascular deaths). More direct trial data on this issue should be forthcoming soon. Crucial to these treatment comparisons is the question of quality of life. All treatment modalities are associated with complications and side effects [3,43]. Set against these are the equally unpleasant effects of progressive disease. This whole area is methodologically difficult, with multiple dimensions of quality to consider (pain, vigour, disability and handicap, psychosexual and social elements) and the competing effects of comorbidity, cancer and treatment. However, it is likely that small differences in quality of life will have a large influence on treatment choice, and so it should not be ignored in future trials and other research. A further aspect will be cost-effectiveness studies. Precise estimates of the relative benefits of treatments can only be derived from randomized trials of

158 sufficient size. If the differences in outcomes are small, the marginal cost of any one treatment over another may not be worthwhile. This may count against conservative management, especially if immediate therapy is shown to be superior and gonadotrophin releasing h o r m o n e agonists or 'total androgen blockade' regimens are used over many years. There may be renewed interest in low dose oestrogens (diethylstilboestrol 1 mg/day), which is very cheap, and which one of the V A C U R G studies hinted might be superior to orchidectomy and was not associated with greater cardiovascular morbidity or mortality [19]. The b o t t o m line is that no treatment modality has been shown to be superior to any other. The pragmatic management option under such conditions of uncertainty is to opt for the least invasive treatment, in this case conservative m a n a g e m e n t or 'watchful waiting'. Given the available evidence, and at risk of running counter to what is now accepted by custom and practice in many parts of the world, radical prostatectomy, radiotherapy and immediate androgen blockade all remain unproven methods of improving survival; as such their use outside of randomized controlled trials may be questioned. Such trials would need to be large. To detect a 10% difference (93% versus 83%) in cancer-specific survival between operation and conservative management, and assuming that the death rate from intercurrent disease is 10% over 10 years (from the surgical series) [20], with 90% power at P = 0.05, would require 240 patients per arm. If non-cancer mortality is actually 30% over 10 years (which matches the V A C U R G surgical trial more nearly) 280 patients are needed per arm. To demonstrate that the size of the benefit was between 8% and 12% (i.e. a more precise estimate of the size of the effect, rather than the mere statistical likelihood that there was a difference) would require 2270 patients per arm.

SUMMARY Prostate cancer is an important and increasing source of male morbidity and mortality. In the absence of any primary preventative strategy, medical approaches to control it will concentrate on attempts at cure in localized disease and effective palliation otherwise. Observational epidemiological studies suggest that, in practice, differences in the effectiveness of aggressive and conservative approaches will be small, but may yet be worthwhile in selected groups of men. However, the confounding and biases inherent in all observational epidemiology mean that the data available from this source is insufficiently certain or precise either to make treatment recommendations for individuals, or to quantify relative benefits to inform health policy. Randomized trial data has not suggested any overwhelming benefit for any one treatment modality, but the five published trials have been small and lacked the statistical power to demonstrate potentially important differences.

R.H. Harwood Aggressive management aimed at cure should be evaluated in adequately designed randomized trials in comparison with expectant medical management ('watchful waiting'). The trials currently planned or under way should be supported enthusiastically by all centres with an interest in management of prostate cancer.

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Announcements September 10--13 1995 SOUTH A F R I C A N SOCIETY M E D I C A L O N C O L O G Y / S O U T H A F R I C A N SOCIETY R A D I A T I O N O N C O L O G Y CONGRESS Location: Thaba Nchu Sun, Free State, South Africa. Further information from: SASMO/SASRO Congress Organiser, PO Box 4345, Bloemfontein 9300, South Africa. Fax: (+27)-52-306-714.

Annual Dinner, The Great Hall, St Bartholomew's Hospital 16 September • Faculty of Clinical Radiology Imaging: Liver, Pituitary, Pancreas; Introduction to Power Doppler; Contrast Agents in Ultrasound

For detailed programme and registration form, please contact: Meeting Secretariat, FJN Associates, 98 Stanley Road, Harrow, Middx HA2 8AZ, Tel/Fax: 0181 423 2656.

September 15-16 1995

November 6-8 1995

THE R O Y A L C O L L E G E O F R A D I O L O G I S T S SCIENTIFIC M E E T I N G A N D A N N U A L G E N E R A L MEETING

MODERN INTERSTITIAL IMPLANT THERAPY TEACHING COURSE

The Royal College of Radiologists will be holding a 1 days' scientific meeting at the Imperial College of Science, Technology and Medicine, London. 15 September • Faculty of Clinical Radiology Renal Angioplasty; Percutaneous Nephrostomy and Ureteric Stenting; Percutaneous Inertion of Central Venous Catheters. Followed by: The Sir Peter Kerley Lecture, Professor D. Cumberland, Sheffield "Coronary Imaging and Intervention: Present and Future"; The Rohan Williams Travelling Professor Lecture, Professor M. S. Khanguare, Perth, Australia, "Embolisation of Brain AVMs". • Faculty of Clinical Oncology Radiotherapy in Benign Disease; Teaching sessions: "Informed Consent in Oncology - Do We Need It?" Dr R. N. Palmer, Medical Protection Society; "Managing Medullablastoma" Dr A. Gray, Riyadh. • Joint Faculty Symposium, "Imaging in Malignant Disease" • Annual General Meeting, Clore Theatre, Imperial College

A three day course which will include lectures and practicals on: Physical properties of 192Ir; Radiation Protection; Radiobiology of High and Low Dose Rate Brachytherapy; Principles of Pulsed Brachytherapy; Organisation and equipment of an Implant Service; Techniques; Dosimetry; Indications; Clinical applications and results. The course will be open to Consultants and Registrars in training and to Physicists but is limited to 30 people. Joint organizers: Dr D. V. Ash (Leeds) and Dr J. R. Owen (Cheltenham). Guest Lecturer: Professor P. Scalliet. Location: Cookridge Hospital, Leeds. Fee: £240 which includes lunches and coffee. Further details and application forms: Dr D. Ash, Cookridge Hospital, Leeds LS16 7QB, UK.

Announcements for these pages should be submitted to: Dr W. G. Jones, Editor, Clinical Oncology, The Royal College of Radiologists, 38 Portland Place, London W1N 3DG, UK. Announcements must be typewritten giving clear and concise details of the date, location and point of contact. Submission deadline: A minimum of four months before the evenL