All-Cause Mortality in Randomized Trials of Cancer

William C. Black, David A. Haggstrom, H. Gilbert Welch of all-cause mortality as the primary end point in cardiac drug Background: The most widely accepted end point in random-
ized cancer screening trials is disease-specific mortality. The
In this article, we review the major randomized trials of can- validity of this end point, however, rests on the assumption
cer screening, point out inconsistencies in their disease-specific that cause of death can be determined accurately. An alter-
and all-cause mortality results, and offer explanations for why native end point is all-cause mortality, which depends only
these inconsistencies may have occurred.
on the accurate ascertainment of deaths and when they oc-
cur. We compared disease-specific and all-cause mortality in

published randomized cancer-screening trials to indirectly
assess the validity of the disease-specific mortality end point.

We obtained a list of randomized trials of cancer screening Methods: We examined all 12 published randomized trials of
from a published authoritative text devoted to this subject (14). cancer screening for which both end points were available
The text cited 16 randomized trials for which disease-specific (seven of mammography, three of fecal occult blood detec-
mortality has been reported. Eight of these trials pertained to tion, and two of chest x-ray screening for lung cancer). For
screening for breast cancer with mammography, three pertained each randomized trial, we subtracted disease-specific mor-
to screening for colorectal cancer with fecal occult blood testing, tality observed in the screened group from that observed in
and five pertained to screening for lung cancer with chest radi- the control group and all-cause mortality in the screened
ography. In addition, we performed an electronic search on group from that in the control group. We then compared the
PubMed (National Library of Medicine) by using authors’ differences in these two mortality measures. Results: In five
names and other relevant terms to obtain updates on these trials.
of the 12 trials, differences in the two mortality rates went in
We excluded four of these randomized trials because neither opposite directions, suggesting opposite effects of screening.
all-cause mortality nor data from which all-cause mortality In four of these five trials, disease-specific mortality was
could be calculated were reported [the Stockholm mammo- lower in the screened group than in the control group,
graphic screening trial (15), the London mass radiology trial whereas all-cause mortality was the same or higher. In two
(16), the Johns Hopkins study (17), and the Memorial Sloan- of the remaining seven trials, the mortality rate differences
Kettering study (18)]. Thus, we found 12 randomized trials of were in the same direction but their magnitudes were incon-
cancer screening for which we could obtain disease-specific andall-cause mortality (19–30): seven of mammography, three of sistent; i.e., the difference in all-cause mortality exceeded the
fecal occult blood, and two of chest x-rays for lung cancer disease-specific mortality in the control group. Thus, results
of seven of the 12 trials were inconsistent in their direction or
For each of these 12 trials, we used the most recent source magnitude. Conclusion: Major inconsistencies were identi-
that allowed us to determine both disease-specific and all-cause fied in disease-specific and all-cause mortality end points in
mortality. For consistency, we reported mortality as the number randomized cancer screening trials. Because all-cause mor-
of deaths per 10 000 person-years of observation and, for each tality is not affected by bias in classifying the cause of death,
randomized trial, we used the same denominator for disease- it should be examined when interpreting the results of ran-
specific and all-cause mortality. For four of the randomized domized cancer-screening trials. [J Natl Cancer Inst 2002;
trials, we obtained mortality rates directly from the source 94:167–73]
(19,27,28,30). For the remaining eight randomized trials, we Disease-specific mortality is the most widely accepted end Affiliations of authors: W. C. Black, Department of Radiology, Dartmouth- point in randomized clinical trials of screening for cancer (1,2). Hitchcock Medical Center, Lebanon, NH, and Department of Community and The validity of this end point, however, rests on the fundamental Family Medicine, Center for the Evaluative Clinical Sciences, Dartmouth Medi- assumption that the cause of death can be determined accurately.
cal School, Hanover, NH; D. A. Haggstrom, Department of Medicine, Dart- This assumption has been seriously challenged by several stud- mouth-Hitchcock Medical Center; H. G. Welch, Department of Medicine, Dart- ies on the accuracy of death certificates (3–9).
mouth-Hitchcock Medical Center, and Department of Community and Family All-cause mortality, in contrast, does not require judgments Medicine, Center for the Evaluative Clinical Sciences, Dartmouth MedicalSchool, and Department of Veterans Affairs Outcomes Group, Department of about the cause of death. Instead, all that this end point requires Veterans Affairs Hospital, White River Junction, VT.
is an accurate ascertainment of deaths and when they occur.
Correspondence to: William C. Black, M.D., Department of Radiology, Dart- Furthermore, all-cause mortality is a measure that can capture mouth-Hitchcock Medical Center, 1 Medical Center Dr., Lebanon, NH 03756 unexpected lethal side effects of medical care. Because of the (e-mail: [email protected]).
concern that some cardiac interventions may cause noncardiac See “Note” following “References.” deaths (10), for example, there has been a trend toward the use Journal of the National Cancer Institute, Vol. 94, No. 3, February 6, 2002 Table 1. Twelve randomized trials of cancer screening reporting both disease-specific and all-cause mortality*
Fecal occult blood
Chest x-ray
*CI ס confidence interval; HIP ס Health Insurance Plan.
†Insufficient data were reported to calculate CIs.
calculated the mortality from the reported number of deaths and ferences in disease-specific mortality were more favorable to- person-years of observation. [Person-years of observation were ward screening than were the differences in all-cause mortality.
reported for four of these randomized trials (21–23,26) but had In five of the 12 trials, the differences were inconsistent in to be approximated by multiplying reported number of subjects direction. In four of these five trials, disease-specific mortality and years of follow-up for the other randomized trials was lower in the screened group than in the control group, whereas all-cause mortality was the same or higher. Among the For each randomized trial, we subtracted disease-specific seven studies in which the differences were in the same direc- mortality observed in the screened group from that observed in tion, the difference in all-cause mortality exceeded the disease- the control group. Similarly, we subtracted the all-cause mortal- specific mortality in the control group in two trials. As is evident ity in the two groups. We compared the differences in these two in Fig. 1, this inconsistency in magnitude was most dramatic for measures of mortality and considered them to be inconsistent if the Edinburgh mammography trial (23). In summary, seven of they satisfied one of two conditions. First, if the differences were the 12 trials had results that were inconsistent in either direction not of the same sign, then we considered the differences to be inconsistent in direction. Second, if the differences were in thesame direction but the difference in all-cause mortality exceeded DISCUSSION
the disease-specific mortality in the control group, then we con- Explanations for Inconsistent Direction
sidered the differences to be inconsistent in magnitude. We rea-soned that screening alone could not explain a deficit in all Although the goal of screening is to prevent deaths from the deaths that exceeded the number of disease-specific deaths, even target disease, screening may affect mortality in other ways. On if screening prevented all disease-specific deaths. Similarly, we the positive side, earlier detection of the target disease could lead reasoned that screening alone would not likely explain an excess to milder treatment and prevent some treatment deaths. In ad- in all deaths that exceeded the number of disease-specific deaths.
dition, screening could prevent deaths from other diseases that We also calculated the 95% confidence intervals (CIs) around are detected earlier incidentally. On the negative side, screening the differences in mortality (31). All P values were from two- could lead to deaths from the evaluation of screening test results sided tests and were based on the Z test for differences in two or from earlier treatment (of the target or other disease) that would not have occurred without screening.
Inconsistency in direction may be partly explained by the inherent ambiguity of disease-specific mortality. Conceptually, Perspective
this end point should include any cause of death that is modified Two observations concerning the mortality rates for 12 by screening, including deaths caused by the target disease, by screening trials are striking (Fig. 1). First, disease-specific mor- treatment of the target disease, and by the screening process.
tality constitutes only a small proportion of all-cause mortality However, the actual rules used to determine which deaths count (3%–16% in the control groups). Second, the differences in all- for disease-specific mortality are rarely published with trial re- cause mortality within each trial are generally small.
sults. Furthermore, the determination of cause of death is a com-plex process that is subject to many sources of error. High rates Inconsistencies
of variation have been demonstrated in the recording of under- Table 1 shows the disease-specific and all-cause mortality in lying cause of death on death certificates, especially when mul- screened and control groups for the 12 trials. Overall, the dif- tiple causes of deaths are involved (3–7). Journal of the National Cancer Institute, Vol. 94, No. 3, February 6, 2002 Fig. 1. Mortality rates in randomized trials of screening for cancers of the breast (A), colon (B), and lung (C) (19–30). HIP ס Health Insurance Plan.
Two biases may explain much of the observed inconsistency can occur in two different ways. First, a death from another in the direction of disease-specific mortality and all-cause mor- cause in the screened group may be falsely attributed to the tality differences (Fig. 2). These biases, which affect only the target cancer because it had previously been diagnosed in the classification of cause of death, occur independently and have subject. Second, a death from the target cancer in the control opposite effects on the reporting of disease-specific mortality.
group may be falsely attributed to another cause because the Sticky-diagnosis bias. Because the target cancer in a screen-
target cancer had not previously been diagnosed in the subject.
ing trial is more likely to be diagnosed in the screened group Although the death-review process in a screening trial can be than in the control group, deaths are more likely to be attributed blinded effectively to randomization, it cannot be blinded com- to the target cancer in the screened group. This misattribution pletely to the diagnosis or treatment of cancer, which can greatly Journal of the National Cancer Institute, Vol. 94, No. 3, February 6, 2002 Fig. 2. Biases affecting disease-specific mortality. It is as-
sumed that screening has no net effect on mortality; i.e.,
screening causes the same number of deaths as it prevents.
For the sticky-diagnosis bias, deaths from other causes in
the screened group are falsely attributed to disease, so that
disease-specific mortality is reportedly higher in the
screened group. For the slippery-linkage bias, deaths from
disease, treatment of disease, or screening process in the
screened group are falsely attributed to other causes, so that
disease-specific mortality is reportedly lower in the
screened group.
influence the subject’s subsequent medical care and record. To slip away from, screening. For example, suppose a subject with the extent that the target cancer diagnosis sticks in the screened screen-detected lung cancer has complications of surgery that group (or another diagnosis sticks in the control group), disease- lead to intensive care. If the subject dies more than 1 month after specific mortality will be biased against screening (32,33). admission, the death might be falsely attributed to another cause, Sticky-diagnosis bias was probably at least partially respon- such as pneumonia. Furthermore, the term disease-specific mor- sible for the excess lung cancer mortality observed in the tality is too restrictive because it does not imply the inclusion of screened group of the Mayo Lung Project, and the misclassifi- deaths from screening in individuals without the target disease, cation was probably most relevant to metastatic adenocarcinoma such as a fatal hemothorax after a percutaneous needle biopsy (30,34). More cases of adenocarcinoma of the lung were diag- for a benign pulmonary nodule. In none of the randomized trials nosed in the intervention group than in the control group (59 reported in Table 1 is it made clear that such deaths from screen- versus 38 cases; P ס .05), and more deaths were attributed to ing are included in the disease-specific mortality end point or this cell type in the intervention group (39 versus 25 cases; P ס how such deaths would have been identified. To the extent that .10). In addition, adenocarcinoma was the only lung cancer cell all these screen-related deaths are misattributed to other causes, type for which case subjects in the screened group had a shorter disease-specific mortality will be biased in favor of screening.
median survival than case subjects in the control group, 1.3 Slippery-linkage bias may be partly responsible for the dis- versus 1.8 years. Lead-time, length, and overdiagnosis biases crepancy in the Minnesota Colon Cancer Control Project (26). In should have prolonged survival in the screened group, even if this study, there were 1.2 fewer deaths per 10 000 person-years early diagnosis had no beneficial effect. Because the primary site from colon cancer in the screening group than in the control of metastatic adenocarcinoma is often difficult to determine, group, but there were 2.1 more deaths per 10 000 person-years some deaths from adenocarcinoma of other organs in the inter- from ischemic heart disease in the screening group. Similar dis- vention group were probably misattributed to lung cancer. In crepancies were observed in the Nottingham trial (27). These addition, some deaths from adenocarcinoma of the lung in the findings raise the possibility that the colon cancer screening or control group were probably misattributed to adenocarcinoma of subsequent treatment may cause some cardiac deaths that are not other organs or other causes because lung cancer had not been properly attributed to the intervention.
Sticky-diagnosis and slippery-linkage biases can both occur Slippery-linkage bias. Many subjects in the screened group
in the same trial, and both probably did in the Mayo Lung may undergo invasive testing for a suspicious screening result, Project (Table 1). However, that all-cause mortality was higher and many others may be treated for early disease. These inter- in the screened group suggests that the slippery-linkage bias was ventions may lead to deaths that are difficult to trace back to, or greater than the sticky-diagnosis bias. Thus, more harm than Journal of the National Cancer Institute, Vol. 94, No. 3, February 6, 2002 benefit was probably obscured by the combination of these two gest that healthier subjects were randomly assigned to the screened group. Large discrepancies in socioeconomic status at All-cause mortality is not affected by sticky-diagnosis and baseline confirm that there was a major imbalance after random- slippery-linkage biases, because it does not depend on the de- ization, which severely threatens the validity of any comparison termination of cause of death. If screening effectiveness (as mea- sured by disease-specific mortality) is obscured because diag- Similarly, in the Czechoslovakian trial of lung cancer screen- noses are sticking, deaths from other causes will be decreased ing (29) (Table 1), the difference in the all-cause mortality be- correspondingly so that all-cause mortality should still reveal a tween the control group and the screened group (25.4 per 10 000 trend toward benefit (albeit not statistically significant). If person-years; P ס .06) was greater than the lung cancer mor- screening harm is obscured because complications are slipping tality in the control group (24.7 per 10 000 person-years). How- away from the intervention, deaths from other causes will be ever, in this trial, the two groups were almost identical imme- increased correspondingly so that all-cause mortality should still diately after randomization. These findings suggest that there was an underreporting of deaths from all causes in the control Statistical considerations. Because the 95% CIs around the
group, biasing the results against screening.
differences in all-cause mortality include zero, all of the incon- Table 2 outlines one possible framework for interpreting vari- sistencies in direction in Table 1 could be the result of chance.
ous combinations of disease-specific and all-cause mortality.
Of course, that such an important end point has relatively wideCIs is an important observation in itself. Nevertheless, these Validity
wide CIs do not imply that chance is the only or even the majorcause of the observed inconsistencies in direction, especially As we have shown, examination of all-cause mortality in when there are plausible alternative explanations.
combination with disease-specific mortality can reveal major The problem with conventional statistics in this setting is threats to the validity of a randomized trial, such as flaws in highlighted by considering a screening intervention that causes randomization and ascertainment of vital status. In addition, all- far more harm than benefit, yet appears to statistically signifi- cause mortality is unaffected by two biases that affect disease- cantly reduce disease-specific mortality. For example, consider a specific mortality—sticky-diagnosis and slippery-linkage biases.
hypothetical trial of screening in which 100 deaths from the To date, the net effect of these biases appears to have favored target cancer and 900 deaths from other causes occur in the screening. In four of the randomized trials where the differences control group. Suppose that screening prevents 30 deaths from have been inconsistent in direction, the disease-specific mortal- the target cancer but causes 90 deaths that are misattributed to ity has been lower in the screened group. This result suggests other causes in the screened group. If we assume 10 000 person- that slippery-linkage bias has been a bigger factor than sticky- years of observation in each arm, then these results could be diagnosis bias and that the harms of screening have been under- reported as a statistically significant 30% reduction in disease- specific mortality (relative risk [RR] ס 0.70; P ס .02) and no Increasing the rigor of the death-review process might help to difference in all-cause mortality (RR ס 1.06; P ס .19).
reduce the effects of slippery-linkage and sticky-diagnosis bi-ases. However, there are two major limitations inherent in the Explanations for Inconsistent Magnitude
death-review process. First, it is difficult to devise a searchstrategy that efficiently identifies all deaths that are plausibly A difference in all-cause mortality that exceeds the disease- related to screening. In the Prostate, Lung, Colorectal and Ovar- specific mortality in the control group is unlikely to be the result ian (PLCO) Cancer Screening Trial (33), which has the most of screening, and this difference cannot be explained by bias in thorough death-review process ever described, the criteria for the classification of the cause of death. Instead, an inconsistency death review include a cancer diagnosis or unknown cause of in magnitude suggests major problems with either randomiza- death. This search strategy would not reliably identify fatal com- tion or the determination of vital status.
plications from an invasive procedure triggered by a false- In the Edinburgh trial of breast cancer screening (23) (Table positive screening test (in a patient who did not have a cancer 1), the difference in all-cause mortality between the control diagnosis), especially if the subject died after being discharged group and screened group (20.1 per 10 000 person-years; from the hospital. Second, even if all the deaths could be re- P<.001) was much greater than the breast cancer mortality in the viewed, assigning cause of death would still be problematic. For control group (5.1 per 10 000 person-years). These results sug- example, if a screened subject had a fatal myocardial infarction Table 2. Interpretations for various combinations of disease-specific mortality and all-cause mortality
All-cause lower, disease-specific not lower Sticky-diagnosis bias: too many deaths attributed to target cancer in the screened group (or too few deaths attributed to target cancer in the control group) All-cause higher, disease-specific not higher Slippery-linkage bias: too few deaths from work-up and treatment attributed to Major flaw in randomization or in ascertainment of vital status No net effect of sticky-diagnosis or slippery-linkage bias All-cause higher, disease-specific higher No net effect of sticky-diagnosis or slippery-linkage bias Journal of the National Cancer Institute, Vol. 94, No. 3, February 6, 2002 after an invasive evaluation, it would be difficult to determine (7) Lloyd-Jones DM, Martin DO, Larson MG, Levy D. Accuracy of death whether the death was caused by the evaluation and, thus, at- certificates for coding coronary heart disease as the cause of death. Ann (8) Newschaffer CJ, Otani K, McDonald MK, Penberthy LT. Causes of death The main argument for using disease-specific mortality in- in elderly prostate cancer patients and in a comparison nonprostate cancer stead of all-cause mortality is that the latter requires far more cohort. J Natl Cancer Inst 2000;92:613–21.
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