Re:Re:Re:Hypnotics' association with mortality or cancer: bias related to the study design and analysis
Dr. Hallas, Dr. Andersen, and colleagues give us the very good news that they are working on a study of benzodiazepine-cancer association using the Danish Cancer Registry. Additional data that isolates benzodiazepine agonists and other hypnotics individually will be very welcome, as different benzodiazepine agonists may have different risks. Perhaps they can provide results from time-dependent Cox models. It will be interesting to see if their time-dependent exposure models can overcome the problems in cohort studies that people not taking hypnotics frequently commence them, whereas hypnotic users frequently discontinue or are intermittent in use.
It now appears that their theory of a bias in selection of our controls does not apply to the dramatic hypnotic mortality hazards that we reported, but only to the overall cancer hazards. Our approach to extraction of hypnotic users from the medical records and matching of a control cohort was designed with mortality in mind. It would require an additional and more difficult extraction of the medical records and a new matching of controls to evaluate the bias they predict in the cancer analyses. A new extraction is unfortunately beyond our resources currently. I see some logic in their argument, but remain skeptical that this theoretical bias could explain the highly-significant dose-response association in overall cancer incidence or the remarkable contrasts between high and low hazards for different cancers.
It would be good if these colleagues with industry sponsorship could arrange controlled hypnotic trials with sufficient exposure to examine mortality and cancer risks. There will always be more concern about biases in analyses of records than in randomized controlled trials.
If hypnotics manufacturers will not sponsor adequate trials to examine the mortality and cancer safety of their drugs, it is necessary for more independent groups to examine these questions in a variety of records systems. Unfortunately, there is so far no evidence that the U.S. Food and Drug Administration or European regulatory agencies will accept their responsibility to protect the public from the most serious risks of hypnotics.
Conflict of Interest:
Please see author Competing Interests in main manuscript.
Re:Re:Hypnotics' association with mortality or cancer: bias related to the study design and analysis
We appreciate the response from Dr. Kripke, although we are afraid it supports our notion of a bias in their selection of reference cohort rather than reassure us about the opposite.
In their study, non-users of hypnotics were required to have no hypnotic prescriptions at any time in their entire follow-up. However, in a cohort study, exposure that occurs after an endpoint should not be taken into consideration. Dr. Kripke asserts that "A patient who developed cancer before receiving a hypnotic would not have been included in either the hypnotic-prescribed or the control group.." These subjects should have been kept in the material as unexposed subjects who developed a cancer. That they are exposed to hypnotics after they develop cancer is irrelevant and should not have been a cause for exclusion. The result is a selective removal of unexposed subjects with an endpoint. There is no corresponding removal of exposed subjects with an endpoint, and the resulting hazard ratio is thus biased upward. As described in our first letter, our simulation exercises suggest that it may explain the elevated hazard ratio for cancers entirely.
We are currently working on a study of the benzodiazepine-cancer association using data from the Danish Cancer Registry, and we expect to have our results made publicly available soon.
Conflict of Interest:
MA and JH has participated in research projects funded by Nycomed, the manufacturer of Nitrazepam, and Pfizer, the manufacturer of Halcion (triazolam) and Tafil (alprazolam), with grants paid to institutions where they have been employed. JH has personally received fees for teaching from Nycomed. AP and SF declare no conflicts of interest.
Re:Hypnotics' association with mortality or cancer: bias related to the study design and analysisReplying to Dr. Andersen and colleagues, we appreciate their very learned statistical comments on our article. First, there seems to be a misunderstanding of our selection criteria. A patient who developed cancer before receiving a hypnotic would not have been included in either the hypnotic-prescribed or the control group, and therefore would not bias the study in regard to hypnotic-associated cancer incidence. Secondly, the comment is correct that we did not use a time-dependent model, which would have had advantages had it been feasible. Since our data indicated when a hypnotic was prescribed but not when the doses were ingested, we thought a time-dependent model would not be feasible and any attempt might be misleading. Although we commented that 18 days of hypnotic exposure would be too soon to have caused a diagnosed cancer, some research suggests that most of us harbor cells in which an undetectable cancer has already been initiated. The question is really whether cancer growth could be promoted that rapidly to the point where the cancer could be detected. We agree that this would be unusual, but of course, Figure 1 in the Data Supplement shows that most of the cancer hazard was manifest 6 months and more after the first hypnotic dosage. Since a patient had to survive about 3 months to be included in the study, terminal patients were excluded. Commentators troubled by the time course of our study may be interested in Kao et al. (Mayo Clin. Proc 2012;87:430-436), which observed a much higher zolpidem hazard for cancer with a longer period of follow-up. Thirdly, as emphasized in the Data Supplement, we experimented with adjusting for comorbidities recognized before the observation period in an unstratified model (as Dr. Andersen and collegues suggested) as well as including comorbidities observed during the observation period in our stratified model, and we examined several additional models for covariate adjustment. None of the alternatives produced meaningful alterations in the hazard ratios. We think we selected an approach which minimized the risk of false-positive biases. We would very much welcome attempts to replicate our findings using Scandinavian data sets which may permit alternative statistical approaches.
Conflict of Interest:
Please see the inital manuscript.
Re:Is it hypnotics that kill, or is it psychiatric illness?In reply to Dr. Terkelsen and colleagues, I am greatly awed by the extensive literature review which they kindly offered with so much effort. Unfortunately, these colleagues ignored the point which we made in our article: Mallon et al. (reference 7) and Belleville (reference 8) have shown that control for depression does not substantially attenuate the mortality hazard associated with hypnotics. On the other hand, Patten et al. (Can J Psychiatry 2011;56:658-666) showed that depression is no longer a significant mortality predictor when hypnotic use is controlled. Many of the depression hazard ratios which Dr. Terkelsen and colleagues offer may have been confounded by failure to control for hypnotic use, but studies of both risk factors show that the hypnotic risk is independent. In any case, the average mortality hazard associated with depression which their review offers was about 1.75, which could not possibly account for the hypnotic-associated hazard ratio of 4.6, considering that not all patients taking hypnotics would have been depressed and not all controls would have been free of depression.
Conflict of Interest:
Please see the original manuscript
Hypnotics' association with mortality or cancer: bias related to the study design and analysis
In BMJ Open, Kripke et al have presented a study on risks associated with the use of hypnotics (1). In their two-in-one study, the authors report an about fourfold increased risk of death and a 35% increased risk of cancer when comparing users of hypnotics with non-users. The authors present the analyses as a cohort study using a survival analysis model with Cox regression. However, several approaches in both the study design and analysis do not fulfil the conditions for a survival analysis, primarily because the authors do not respect the time sequence of exposure and events. We believe it is important to draw attention to these limitations, because the applied approaches are likely to have introduced bias that may have contributed substantially to the findings.
Firstly, the main criterion for being selected as a non-user is that the study subject has not redeemed any prescriptions for hypnotics anytime during the entire study period. If we have understood this correctly, the consequence of this exposure criterion is that study subjects who received their first hypnotic dispensing after a cancer diagnosis, something reasonable and quite common (2), were excluded from the reference group. These cancer events were, however, occurring among non-exposed study subjects and should be included among these. The selective exclusion creates a spurious association between hypnotics and cancer, with a magnitude depending on the incidence of hypnotic use among cancer patients. A calculation suggests that a cumulative incidence of hypnotic use of 25% among cancer patients would create a 30% spuriously elevated cancer risk through this mechanism. Kripke et al's design violates one of the fundamentals of cohort study design: one should not base the exposure definition on future events - "you should never use a crystal ball".
Secondly, Kripke et al did not use a time-dependent exposure model. Hypnotic exposure began at the time of first prescription and an average exposure was calculated over the entire observation period to either censoring or occurrence of an outcome event. Among persons with a low average exposure we would expect a considerable proportion of "remote users", i.e., persons with only few dispensings who may not even have been exposed at the time of cancer or death. The more than three-fold increased risk of death observed for the lowest average dose level could imply that use of hypnotics was a marker of some underlying condition (e.g., psychiatric disease) that the analysis was not able to adjust for rather than the cause of death per se. A model with time-dependent exposure classification would provide more information on the relationship between exposure patterns and risk.
Similarly, in the cancer substudy, a dose-response analysis based on the average amount of dispensed hypnotics was performed, but analyses taking into account exposure duration and time-dependent cumulative exposure were not presented. We consider the latter analyses essential for evaluating the plausibility of a causal effect. The authors exclude study subjects where cancer is diagnosed less than 18 days from exposure, which they state is "too soon after for it to be at all plausible that the hypnotic caused the cancer". This period is much too short. A sensitivity analysis excluding exposure in different time intervals close to the cancer diagnosis would have been informative regarding the potential prescribing of hypnotics related to early symptoms of the cancer (reverse causation bias) or sleep disturbances during the diagnostic work-up for cancer. A similar pattern might be occurring in the mortality analysis; subjects may have used small quantities of hypnotics to treat distress over a fatal disease shortly before their death. Unfortunately, Kripke et al do not account for the temporal pattern, which renders the paper difficult to interpret.
Thirdly, when adjusting for confounding, Kripke et al used information on comorbidity from the entire observation period, i.e., both before and after start of hypnotic exposure. Usually, adjusting for covariates observed during the entire period from exposure to outcome event(s) is discouraged, because it may induce bias, unless a model reflecting time-dependent exposure is used (3, 4). With the approach applied in the present study, the amount of information on confounders accumulates over time. This could lead to impaired adjustment for confounding among those who leave the study cohorts early. We note that there was very little difference between crude and adjusted estimates. This could imply lack of confounding, but also that the adjustment was deficient. An additional reason for inefficient confounder control despite the thorough matching could be that comorbidity was defined in rather broad categories. One way of evaluating confounders would be to examine associations between confounders and outcome, but the use of a comorbidity -stratified Cox model unfortunately obscures this possibility.
In summary, we believe that the associations between hypnotic use and cancer or death in the study by Kripke et al may to a large degree be explained by selection bias affecting the controls, and to a lesser degree by suboptimal control of confounding. Kripke et al may inadvertently have introduced bias by some of the choices they have made in their study design and analysis. Furthermore, analyses taking into account time- dependent exposure and - in the analysis of cancer risk - both exposure duration and cumulative exposure would have added much to the interpretation of results.
Finally, we would like to add that we share the authors' view on hypnotics in general. Prescription of hypnotics should generally be avoided, and these drugs should almost exclusively be reserved for short- term use in selected patients.
1. Kripke DF, Langer RD, Kline LE. Hypnotics' association with mortality or cancer: a matched cohort study. BMJ Open 2012;2:e000850. doi:10.1136/bmjopen-2012-000850
2. Casault L, Savard J, Ivers H, Savard M-H, Simard S. Utilization of hypnotic medication in the context of cancer: predictors and frequency of use. Support Care Cancer 2012; 20:1203-10.
3. Wolfe RA, Strawderman RL. Logical and statistical fallacies in the use of Cox regression models. Am J Kidney Dis 1996;27(1):124-9.
4. van Walraven C, Davis D, Forster AJ, Wells GA. Time-dependent bias was common in survival analyses published in leading clinical journals. J Clin Epidemiol 2004;57(7):672-82.
Conflict of Interest:
MA and JH has participated in research projects funded by Nycomed, the manufacturer of Nitrazepam, and Pfizer, the manufacturer of Halcion (triazolam) and Tafil (alprazolam), with grants paid to institutions where they have been employed. JH has personally received fees for teaching from Nycomed. AP and SF declare no conflicts of interest.
Is it hypnotics that kill, or is it psychiatric illness?
Is it hypnotics that kill, or is it psychiatric illness? * Kenneth G. Terkelsen, M.D. General Psychiatrist, Assistant Director * James P. McGuire, M.D. Child and Adolescent Psychiatrist Behavioral Health Services Community Health Center of Cape Cod Mashpee, Massachusetts, USA
* Michael B. Friedman, Adjunct Associate Professor Columbia School of Social Work and Mailman School of Public Health New York, New York, USA Kripke et al. (1) raised an important concern in reporting high mortality in people using zolpidem and similar hypnotics. Already, several patients in our community health center have asked whether zolpidem is going to kill them. One primary care provider here now refuses to prescribe zolpidem citing this report and counseling his patients about the dangers of these medications. These concerns and decisions led us to read the paper, along with related studies, to settle the issue for ourselves. Although the claim that, "in 2010, hypnotics may have been associated with 320 000 to 507 000 excess deaths in the USA alone," is alarming and most certainly deserves further study, as it stands, this report is not a secure foundation for clinical decision-making about the use of hypnotics because it does not control for psychiatric and substance use disorders. Contributions of depression, anxiety and substance use disorders to mortality in primary care. In the last paragraph of Discussion, the authors disclose that, "we were unable to control for depression, anxiety and other emotional factors because of Pennsylvania laws protecting the confidentiality of those diagnoses," and that, "our findings might reflect some confounding by those conditions." While alcohol and tobacco use disorders were addressed, there is no mention of contributions to mortality from opioid, cocaine, cannabis or other psychoactive use conditions in this report. Although psychiatric and substance use conditions are not likely to be the only uncontrolled confounds in this study, it is prudent to consider the effects of these conditions, since they are very common in primary care. Others who have reported elevated mortality hazard in people given hypnotics have spelled this out quite clearly. Mallon et al. (2) reported a risk ratio of 3.285 for hypnotic use, but went on to state, "the increased mortality found among hypnotic users in this study may in fact be related to underlying diseases and their management rather than the hypnotic medication used." In our view, failure to control for psychiatric conditions, including most substance abuse and dependence conditions, should constrain practitioners from employing Kripke et al.'s findings for clinical decision support and policy development in primary care settings. Depression, insomnia and mortality related to other medical conditions. In the remainder of our remarks, we focus on depression since interaction of depression with other medical conditions has been extensively studied. Here are the major findings related to the issue addressed by Kripke et al.(1): 1. Depression is common in people attending primary care settings. Using conservative diagnostic criteria equivalent to the DSM-IV definition of major depressive episode, several recent studies have shown current rates of serious depression in primary care practices that exceed those seen in general population surveys. Ansseau et al. (3) reported that 6.3 percent of people visiting general practitioners in Belgium met DSM-IV criteria for depression. Ostler et al. (4) reported a rate of 7.2% for probable depression using the HADS among 18 414 people attending 55 representative practices in Hampshire. Wittchen et al. (5) identified major depressive episodes in 6.0 percent of 20 000 people attending 558 primary care practitioners in Germany. While screening 18 456 primary care attendees in typical primary care waiting rooms in six international cities, Simon et al. (6) found that 6.5 percent of subjects met the DSM-IV criteria for current depressive episode. 2. Depression is present in a majority of people currently reporting insomnia in primary care. Insomnia is generally considered a risk factor for development of depression (7). In a survey just published, depression was present in 50 percent of primary care patients who reported difficulty sleeping. (8) Young people reporting insomnia are 4 times more likely than those without insomnia to report depression at 3.5 year follow-up. (9) 3. Insomnia is present in an overwhelming majority of people with depression. In cross-national studies of the epidemiology of depression, insomnia was the most commonly reported symptom of depression. (10) In a representative sample of people in metropolitan Toronto interviewed by telephone, insomnia was present in 75.5 percent of people who met DSM-IV criteria for any current mood disorder. (11) We hypothesize that many patients seen in primary care who complain about insomnia are suffering from depression which goes unrecognised and untreated since they do not mention other depressive symptoms and their practitioners do not ask about these other symptoms. We also hypothesize that unrecognised and/or untreated depression contributes more to the increased mortality of people taking hypnotics than do the hypnotics themselves. In the NIMH ECA longitudinal surveys of prevalence of psychiatric disorders, (12) the odds ratio for depression was 35.0 in people with current insomnia, but only 1.6 in people who reported insomnia at baseline but no longer had insomnia at follow-up. (13) Comparing associations between chronic insomnia and depression in two surveys of the same population 11 years apart, Neckelmann et al. (14) found that only those with insomnia at follow-up had a significant increase in depression (OR=1.8). If our hypotheses are correct, we should be able find associations between depression and mortality in studies of outcomes in all the major illness categories studied by Kripke et al.(1) We reviewed literature of the last 10 years relating depression to mortality in the 12 general illness categories reported by Kripke et al.(1), and for cancer and all-cause mortality. To do this, we searched MedLine for the MESH terms "depression" and "mortality" in addition to MESH terms representing each major illness category. For example, we searched for "depression" and "mortality" and "asthma" and so forth for each major illness category. We found that for 11 of these illness classes, as well as for cancer and all-cause mortality, morbidity and/or mortality hazard ratios were elevated in subjects with markers of depression. Some of the recent papers reporting on depression and mortality for specific illness classes are given in Table 1.(18-49) Comparative effects on health outcomes. The importance of controlling for depression is highlighted by a recent study (15) in which mortality associated with depression (HR = 1.52) was comparable to that for smoking (HR = 1.59) Anhedonia may be more deleterious than sadness. Two recent studies shed particular light on what features of depression might heighten mortality. In a study of one-year outcomes following acute coronary syndromes, anhedonia, but not sadness, correlated with mortality. (16) In another recent study, the increased risk of death (HR = 1.31) in people with depression and coronary heart disease disappeared after controlling for self-reported physical activity. (17) Taken together, these findings suggest that by compromising healthy life style choices, self-care and help seeking behaviors, anhedonia and related phenomena (apathy, anergia, abulia) contribute to mortality of depression in people with other major illnesses. This is especially important because anhedonia is more likely to be overlooked, in primary care settings than overt sadness, thus contributing to the failure to recognise and treat depression. How anhedonia might impact on outcomes in medically ill patients. These studies call to mind the many people we treat for depression in our community health center, who very often report things like this: - "When I am depressed, I don't do anything. I don't want to do anything." - "I think of things I should do, but I don't have any get up and go." - "I don't care about anything when I am like this." - "I cringe when the phone rings, and I often don't call back when friends leave a message." - "When neighbors walk by, I go inside." - "I didn't get the mail for weeks. Then the mailman came to the door because there was no more room in the box." Typically and to varying degrees, seriously depressed people are also lax in taking regular exercise, in filling prescriptions and taking medications, even for major medical conditions. Cleaning up around the house, bathing and showering, brushing teeth, and preparing nutritionally adequate meals similarly suffer from neglect. To sum up, although Kripke et al.(1) studied people given hypnotics for insomnia, findings in large population epidemiological studies require us to suspect that insomnia was a symptom of depression, or another psychiatric condition, or a substance use condition which, due to local confidentiality laws, was not discoverable by the research team. So also, we must suspect that, for most illness categories, the mortality of hypnotic use was a proxy for the mortality of psychiatric and substance use conditions in people with major medical illness, acting primarily through diminished self-care and help-seeking behaviors and eventuating in increased mortality due to their co-morbid medical conditions . The real killer is not the over-use of hypnotics, but the under-treatment of depression and other psychiatric conditions and substance abuse conditions in primary care. Conflicts of interest: None reported References (1) Kripke 2012: Kripke DF, Langer RD, Kline LE. Hypnotics' association with mortality or cancer: a matched cohort study. BMJ Open 2012;2:e000850. Print 2012. (2) Mallon L, Broman JE, Hetta J. Is usage of hypnotics associated with mortality? Sleep Med 2009;10:279-86 (3) Ansseau M, Fischler B, Dierick M, et al. Prevalence and impact of generalized anxiety disorder and major depression in primary care in Belgium and Luxemburg: the GADIS study. Eur Psychiatry 2005;20:229-35. (4) Ostler K, Thompson C, Kinmonth AL. Influence of socio-economic deprivation on the prevalence and outcome of depression in primary care: the Hampshire Depression Project. Br J Psychiatry 2001;178:12-7. (5) Wittchen HU, Kessler RC, Beesdo K. Generalized anxiety and depression in primary care: prevalence, recognition, and management. J Clin Psychiatry 2002;63 Suppl 8:24-34. (6) Simon GE, Fleck M, Lucas R, et al. Prevalence and predictors of depression treatment in an international primary care study. Am J Psychiatry 2004;161:1626-34. (7) Lustberg L, Reynolds CF. Depression and insomnia: questions of cause and effect. Sleep Med Rev 2000;4:253-262. (8) Arroll B, Fernando A 3rd, Falloon K, et al. Prevalence of causes of insomnia in primary care: a cross-sectional study. Br J Gen Pract 2012;62:99-103. (9) Breslau N, Roth T, Rosenthal L, et al. Sleep disturbance and psychiatric disorders: a longitudinal epidemiological study of young adults. Biol Psychiatry 1996;39:411-8. (10) Weissman MM, Bland RC, Canino GJ et al. Cross-national epidemiology of major depression and bipolar disorder. JAMA 1996;276:293-9. (11) Ohayon MM, Shapiro CM, Kennedy SH. Differentiating DSM-IV anxiety and depressive disorders in the general population: comorbidity and treatment consequences. Can J Psychiatry 2000;45:166-72. (12) Regier DA, Myers JK, Kramer M, et al. The NIMH Epidemiologic Catchment Area program. Historical context, major objectives, and study population characteristics. Arch Gen Psychiatry 1984;41:934-41. (13) Ford DE, Kamerow DB. Epidemiologic study of sleep disturbances and psychiatric disorders. An opportunity for prevention? JAMA 1989;262:1479- 84. (14) Neckelmann D, Mykletun A, Dahl AA. Chronic insomnia as a risk factor for developing anxiety and depression. SLEEP 2007 30:873-80. (15) Mykletun A, Bjerkeset O, Overland S, et al. Levels of anxiety and depression as predictors of mortality: the HUNT study. Br J Psychiatry 2009;195:118-25. (16) Davidson KW, Burg MM, Kronish IM, et al. Association of anhedonia with recurrent major adverse cardiac events and mortality 1 year after acute coronary syndrome. Arch Gen Psychiatry 2010;67:480-8. (17) Whooley MA, de Jonge P, Vittinghoff E, et al. Depressive symptoms, health behaviors, and risk of cardiovascular events in patients with coronary heart disease. JAMA 2008;300:2379-88. Table 1: Depression's Impact on Outcomes in Major Physical Illness 1. Asthma and Depression. (18) Jiang CQ, Loerbroks A, Lam KB, et al. Mental Health and Asthma in China: the Guangzhou Biobank Cohort Study. Int J Behav Med 2012; Feb 2. [Epub ahead of print, not in March 2012 issue] Compared to those without depression, the prevalence of asthma was higher in those with moderate or severe depression levels (PR?=?2.63, 95% CI?=?1.58-4.40 and PR?=?4.43, 95% CI?=?1.62-12.09, p for trend ?0.0001). The prevalence of asthma increased by 46% with every 1 standard deviation increase of the GDS-C score (PR?=?1.46, 95% CI?=?1.24-1.7 (19) Trzci?ska H, Przybylski G, Koz?owski B, et al. Analysis of the relation between level of asthma control and depression and anxiety. Med Sci Monit 2012;18(3):CR198-202. Individuals with depression were characterized by a significantly lower degree of asthma control compared to depression-free individuals (p<0.001). The degree of asthma control decreased significantly with increasing severity of depression (R=-0.367; p<0.001). 2. Cerebrovascular Disease and Depression. (20) Allan LM, Rowan EN, Firbank MJ, et al. Long term incidence of dementia, predictors of mortality and pathological diagnosis in older stroke survivors. Brain 2011;134:3716-27. Univariate and multivariate regression analyses showed that the most robust predictors of dementia (HR = 1.13) and death (HR = 1.06) in non- demented stroke survivors >75 years of age included (1) low (1.5 standard deviations below age-matched control group) baseline Cambridge Cognitive Examination executive function and memory scores, (2) Geriatric Depression Scale score and (3) three or more cardiovascular risk factors. The mechanism by which depression leads to poor survival, and its interaction with dementia, urgently require further investigation. (21) Pan A, Sun Q, Okereke OI, et al. Depression and risk of stroke morbidity and mortality: a meta-analysis and systematic review. JAMA 2011;306:1241-9. Depression is associated with a significantly increased risk of stroke (HR = 1.25) and fatal stroke (HR = 1.55) in 317 540 cases included in this metanalysis of 28 prospective studies. (22) Ried LD, Jia H, Feng H, et al. Selective serotonin reuptake inhibitor treatment and depression are associated with poststroke mortality. Ann Pharmacother. 2011;45:888-97. Depression diagnosis was associated with greater risk of stroke mortality (HR 1.87; 95% CI 1.24 to 2.82). 3. Coronary Heart Disease and Depression. (23) Connerney I, Sloan RP, Shapiro PA, et al. Depression is associated with increased mortality 10 years after coronary artery bypass surgery. Psychosom Med 2010;72:874-81. Depression, assessed by structured interview and BDI was significantly associated with elevated cardiac mortality (HR = 1.8) ten years after CABG surgery (24) Ahto M, Isoaho R, Puolijoki H, et al. Stronger symptoms of depression predict high coronary heart disease mortality in older men and women. Int J Geriatr Psychiatry 2007;22:757-63. The Kaplan-Meier survival curves showed stronger symptoms of depression to be related to high risks of mortality from CHD or MI among men and women without CHD at baseline and followed for 12 years. According to the Cox model for men significant predictors for higher risk of CHD or MI mortality were stronger symptoms of depression, higher age and a large number of medications in use. (25) Prescott E, Holst C, Gr?nbaek M, et al. Vital exhaustion as a risk factor for ischaemic heart disease and all-cause mortality in a community sample. A prospective study of 4084 men and 5479 women in the Copenhagen City Heart Study. Int J Epidemiol 2003;32:990-7. The 17 items on the vital exhaustion questionnaire were frequently endorsed with prevalence ranging from 6 to 47 per cent, higher in women. All but 4 of the 17 items were significantly associated with IHD with significant relative risks (RR) ranging between 1.36 (95% CI: 1.08, 1.72) and 2.10 (95% CI: 1.63, 2.71). Associations with all-cause mortality were also observed, but were weaker. RR of both IHD and all-cause mortality increased with increasing item sum score and were similar in men and women. For IHD, RR reached a maximum of 2.57 (95% CI: 1.65, 4.00) for subjects endorsing >9 items. The similar RR for all-cause mortality was 2.50 (95% CI: 2.09, 2.99) 4. Chronic Kidney Disease and Depression. (26) Halen NV, Cukor D, Constantiner M, et al. Depression and mortality in end-stage renal disease. Curr Psychiatry Rep 2012;14:36-44. Depression is the most prevalent co-morbid psychiatric condition, estimated at about 25% of end-stage renal disease samples. (27) Kellerman QD, Christensen AJ, Baldwin AS, et al. Association between depressive symptoms and mortality risk in chronic kidney disease. Health Psychol 2010;29:594-600. Mortality HR = 1.24 for people exceeding mean depression ratings by one SD who had mild CKD at baseline and were followed for mean 81 months or until death. After controlling for relevant mortality risk factors (i.e., age, gender, presence of diabetes and cardiovascular disease, and potassium level), results of Cox regression analyses indicated that higher levels of non-somatic depression symptoms were predictive of an increased mortality risk, ??(1, N = 359) = 8.02, p = .005. Patients with non-somatic depression scores 1 SD above the mean had an estimated mortality rate 21.4% higher than average scorers in this sample. (28) Hedayati SS, Minhajuddin AT, Afshar M, et al. Association between major depressive episodes in patients with chronic kidney disease and initiation of dialysis, hospitalization, or death. JAMA 2010;303:1946-53. The presence of an MDE was associated with an increased risk of poor outcomes in CKD patients who were not receiving dialysis, independent of comorbidities and kidney disease severity. The mean (SD) time to the composite event was 206.5 (19.8) days (95% CI, 167.7-245.3 days) for those with an MDE compared with 273.3 (8.5) days (95% CI, 256.6-290.0 days) for those without an MDE (P = .003). The adjusted hazard ratio (HR) for the composite event for patients with an MDE was 1.86 (95% CI, 1.23-2.84). An MDE at baseline independently predicted progression to dialysis (HR, 3.51; 95% CI, 1.77-6.97) and hospitalization (HR, 1.90; 95% CI, 1.23-2.95). (29) Hedayati SS, Jiang W, O'Connor CM, et al. The association between depression and chronic kidney disease and mortality among patients hospitalized with congestive heart failure. Am J Kidney Dis 2004;44:207- 15. After controlling for important clinical factors, severe CKD was associated with depressive symptoms by BDI (odds ratio, 2.89; 95% confidence interval, 1.39 to 5.99). Both depression by DIS and severe CKD were significant predictors of mortality. The increased mortality risk associated with depression did not decline with decreasing kidney function. 5. Chronic Obstructive Pulmonary Disease and Depression. (30) De Voogd JN, Wempe JB, Ko?ter GH, et al. Depressive symptoms as predictors of mortality in patients with COPD. Chest 2009;135:619-25 Depressive symptoms (odds ratio [OR], 1.93; 95% confidence interval [CI], 1.12 to 3.33) were associated with mortality in patients with COPD, independent of other factors including male sex (OR, 1.73; 95% CI, 1.03 to 2.92), older age (OR, 1.05; 95% CI, 1.02 to 1.08), and lower Wpeak (OR, 0.98; 95% CI, 0.97 to 0.99). (31) Ng TP, Niti M, Tan WC, et al. Depressive symptoms and chronic obstructive pulmonary disease: effect on mortality, hospital readmission, symptom burden, functional status, and quality of life. Arch Intern Med 2007;167:60-7. Multivariate analyses showed that depression was significantly associated with mortality (hazard ratio, 1.93; 95% confidence interval, 1.04-3.58), longer index stay (mean, 1.1 more days; P = .02) and total stay (mean, 3.0 more days; P = .047), persistent smoking at 6 months (odds ratio, 2.30; 95% confidence interval, 1.17-4.52), and 12% to 37% worse symptoms, activities, and impact subscale scores and total score on the St George Respiratory Questionnaire at the index hospitalization and 1 year later, even after controlling for chronicity and severity of COPD, comorbidities, and behavioral, psychosocial, and socioeconomic variables. (32) Stage KB, Middelboe T, Pisinger C. Depression and chronic obstructive pulmonary disease (COPD). Impact on survival. Acta Psychiatr Scand 2005;111:320-3. Depression in out-patients suffering from COPD appears to be an independent protector for mortality. 6. Diabetes Mellitus and Depression. (33) Milano AF, Singer RB. Mortality in co-morbidity (II)--excess death rates derived from a follow-up study on 10,025 subjects divided into 4 groups with or without depression and diabetes mellitus. J Insur Med 2007;39:160-6. Mortality for diabetics with depression was 1.70 fold higher than death rate expected for diabetes alone. (34) Young BA, Von Korff M, Heckbert SR, et al. Association of major depression and mortality in Stage 5 diabetic chronic kidney disease. Gen Hosp Psychiatry 2010;32:119-24. Major depression at baseline was associated with a 2.95-fold greater risk of mortality among stage 5 CKD diabetic patients. Given the high mortality risk, further testing of targeted depression interventions should be considered in this population. (35) Pan A, Lucas M, Sun Q, et al. Increased mortality risk in women with depression and diabetes mellitus. Arch Gen Psychiatry 2011;68:42-50. Compared with participants without either condition, the age-adjusted relative risks (RRs) (95% confidence interval) for all-cause mortality were 1.76 (1.64-1.89) for women with depression only, 1.71 (1.54-1.89) for individuals with diabetes only, and 3.11 (2.70-3.58) for women with both conditions. The corresponding age-adjusted RRs of CVD mortality were 1.81 (1.54-2.13), 2.67 (2.20-3.23), and 5.38 (4.19-6.91), respectively. 7. Heart Failure and Depression. (36) Sherwood A, Blumenthal JA, Hinderliter AL, et al. Worsening depressive symptoms are associated with adverse clinical outcomes in patients with heart failure. J Am Coll Cardiol 2011;57:418-23. Worsening symptoms of depression are associated with a poorer prognosis in HF patients, HR = 1.10 for mortablity or CV hospitalization. (37) Kato N, Kinugawa K, Yao A, et al. Relationship of depressive symptoms with hospitalization and death in Japanese patients with heart failure. J Card Fail 2009;15:912-9. Multivariate Cox regression analyses indicated that depressive symptoms were predictors of cardiac death or HF hospitalization (hazard ratio [HR], 3.29; P = .02), HF hospitalization (HR, 3.36; P = .04), and all-cause death (HR, 5.52; P = .01), independent of age and brain natriuretic peptide. (38) de Denus S, Spinler SA, Jessup M, et al. History of depression as a predictor of adverse outcomes in patients hospitalized for decompensated heart failure. Pharmacotherapy 2004;24:1306-10. The 34 patients with a history of depression had a higher likelihood of experiencing the combined end point of in-hospital death or CPR compared with the 137 patients without a history of depression (17.7% vs 6.6%, p<0.05). A history of depression (odds ratio 3.3, 95% confidence interval 1.01-10.6, p<0.05) was still predictive of in-hospital death or CPR in a multivariate analysis after adjusting for predictors of the combined end point. 8. Hypertension and Depression. (39) Kuo PL, Pu C. The contribution of depression to mortality among elderly with self-reported hypertension: analysis using a national representative longitudinal survey. J Hypertens 2011;29:2084-90. In the full model, the hazard ratios for mortality for the groups of not hypertensive/depressed, hypertensive/not depressed, and hypertensive/depressed were 1.12 [95% confidence interval (CI) 0.98-1.28], 1.32 (95% CI 1.19-1.46), and 1.54 (95% CI 1.29-1.83), respectively, compared with the reference group of not hypertensive/not depressed. (40) Peters R, Pinto E, Beckett N, et al. Association of depression with subsequent mortality, cardiovascular morbidity and incident dementia in people aged 80 and over and suffering from hypertension. Data from the Hypertension in the Very Elderly Trial (HYVET). Age Ageing 2010;39:439-45. For GDS >= 6, a strong association was found between baseline depression scores and later fatal and non-fatal cardiovascular endpoints over a mean follow-up of 2 years in a hypertensive very elderly group (all cause mortality HR = 1.8, cardiovascular mortality HR = 2.10, all stroke mortality HR = 1.8) 9. Obesity and Depression. (41) Acosta-P?rez E, Canino G, Ram?rez R, et al. Do puerto rican youth with asthma and obesity have higher odds for mental health disorders? Psychosomatics 2012;53:162-71. Epub 2012 Jan 28. Asthma and obesity were significantly related to higher odds of depressive/anxiety disorders in youth. 10. Reflux / Peptic Disease and Depression. No references found 11. Peripheral Vascular Disease and Depression. (42) Cherr GS, Zimmerman PM, Wang J, et al. Patients with depression are at increased risk for secondary cardiovascular events after lower extremity revascularization. J Gen Intern Med 2008;23:629-34. At revascularization, 35.0% patients had been diagnosed with depression. Those with depression were significantly younger and more likely to use tobacco. By life-table analysis, patients with depression had significantly increased risk for death/MACE, coronary heart disease, and contralateral PAD events, but not cerebrovascular events or death. By multivariate analysis, patients with depression were at significantly increased risk for death/MACE (hazard ratio [HR] = 2.05; p < .0001), contralateral PAD (HR = 2.20; p = .009), and coronary heart disease events (HR = 2.31; p = .005) but not cerebrovascular events or death. (43) Cherr GS, Wang J, Zimmerman PM, et al. Depression is associated with worse patency and recurrent leg symptoms after lower extremity revascularization. J Vasc Surg 2007;45:744-50. Depression is common among patients undergoing intervention for symptomatic PAD. After intervention, patients with depression have worse outcomes for the affected leg. By multivariate analysis, patients with depression were at significantly increased risk for recurrent symptomatic PAD (hazard ratio [HR], 1.77; 95% confidence interval [CI], 1.03 to 3.02; P = .04) and failure of revascularization (HR, 2.18; 95% CI, 1.22 to 3.88; P < .01), but not major amputation. 12. All-cause Mortality and Depression. (44) Mykletun A, Bjerkeset O, Overland S, et al. Levels of anxiety and depression as predictors of mortality: the HUNT study. Br J Psychiatry 2009;195:118-25. Case-level depression was associated with increased mortality (hazard ratio (HR) = 1.52, 95% CI 1.35-1.72) comparable with that of smoking (HR = 1.59, 95% CI 1.44-1.75), and which was only partly explained by somatic symptoms/conditions. (45) Mykletun A, Bjerkeset O, Dewey M, et al. Anxiety, depression, and cause-specific mortality: the HUNT study. Psychosom Med 2007;69:323-31. Depression is a risk factor for all major disease-related causes of death and nearly all major causes of death; the association between depression and mortality was no stronger for CVD mortality than for other causes combined. (46) Prescott E, Holst C, Gr?nbaek M, et al. Vital exhaustion as a risk factor for ischaemic heart disease and all-cause mortality in a community sample. A prospective study of 4084 men and 5479 women in the Copenhagen City Heart Study. Int J Epidemiol 2003;32:990-7. The 17 items on the vital exhaustion questionnaire were frequently endorsed with prevalence ranging from 6 to 47 per cent, higher in women. All but 4 of the 17 items were significantly associated with IHD with significant relative risks (RR) ranging between 1.36 (95% CI: 1.08, 1.72) and 2.10 (95% CI: 1.63, 2.71). Associations with all-cause mortality were also observed, but were weaker. RR of both IHD and all-cause mortality increased with increasing item sum score and were similar in men and women. For IHD, RR reached a maximum of 2.57 (95% CI: 1.65, 4.00) for subjects endorsing >9 items. The similar RR for all-cause mortality was 2.50 (95% CI: 2.09, 2.99) (47) Fu CC, Lee YM, Chen JD. Association between depressive symptoms and twelve-year mortality among elderly in a rural community in Taiwan. J Formos Med Assoc 2003;102:234-9. Of the 280 study participants, 94 died within the 12-year study period. Univariate analysis revealed the following significant predictors of mortality: advanced age, type of household, marital status, and CES-D score. The multivariate age-adjusted hazard ratio for depressive symptoms (CES-D score >/= 15 vs < 15) was 1.55 (95% confidence interval, 0.99 to 2.44). (48) Ensinck KT, Schuurman AG, van den Akker M, et al. Is there an increased risk of dying after depression? Am J Epidemiol 2002;156:1043-8. 68,965 patients were followed for an average of 15 years. Among 1,362 depressed subjects 132 died, and among 67,603 non-depressed subjects 4,256 died. The adjusted hazard ratio for depressed versus non-depressed subjects was 1.39 (95% confidence interval: 1.16, 1.65). 13. Cancer and Depression. (49) Onitilo AA, Nietert PJ, Egede LE. Effect of depression on all-cause mortality in adults with cancer and differential effects by cancer site. Gen Hosp Psychiatry 2006;28:396-402. Compared to the reference group, the hazard ratios (HRs) for all-cause mortality were as follows: cancer but no depression HR = 1.43, depression but no cancer HR = 1.44, cancer and depression HR = 1.87.
Conflict of Interest:
Re:Conflict of interest: response to Ms Colella
Please note that my co-authors have approved our manuscript, but Dr. Langer and Dr. Kline have no previous publications about hypnotic drugs and no affiliation with the www.DarkSideOfSleepingPills.com web site. Some people would think it scientifically proper that I participated in a new study which overcomes some of the limitations of my previous scientific studies, along with co-authors who have no previous biases or financial interests.
Perhaps if she has not finished her training, Ms Colella does not realize that currently, neither the hypnotic manufacturers nor pharmacists are providing U.S. patients with warnings about the mortality and cancer risks of hypnotic drugs. It is not as if these risks were previously unknown, since there are the 18 previous studies. Does the fact that my non-profit web site costs me money constitute "blatant conflict of interest"? Who then is to provide the warnings, if not a co-author of previous studies involving almost 2 million participants? The previous studies also showed mortality and cancer risks. How would Ms Colella warn patients of a 4.6-fold mortality risk and a risk of cancer without scaring them, or has she evidence that there is nothing for patients to be afraid of? Wouldn't Ms Colella think that if there are 500,000 deaths a year in the U.S. associated with use of hypnotics--an estimate that nobody has questioned--that there might be an ongoing atrocity that we should be worried about, even if we cannot be certain of the magnitude of the causal risk?
Conflict of Interest:
See disclosure in the original article.
Conflict of interest
Dear Editor: I appreciated and read Dr. Kripke's manuscript with interest. He and his co-authors present many considerations healthcare providers should acknowledge when prescribing hypnotics. Hypnotics, like all medications, have inherent risks. I was disappointed however, to read about Dr. Kripke's affiliation, or hosting, of the website www.DarkSideOfSleepingPills.com. In my opinion, this affiliation casts a significant bias on the study outcomes. One click to Dr. Kripke's website clearly reveals his agenda of discrediting the utility of hypnotics. This blatant conflict of interest negates any credible evidence presented in his study. Yes, hypnotics may be overused and yes, there may be better ways to improve sleep, but scare tactics and biased studies should not be employed to advance that cause.
Conflict of Interest:
Propensity score matching to minimize confounding by indicationThe authors made a concerted effort to control for confounding in the design and analysis phase of this paper, and correctly stated that unmeasured confounding is a limiting feature of the results. Given the understandable concerns about confounding by indication, another approach the authors may wish to consider is propensity score matching for the analysis. Indeed, they should be able to show that a given hypnotic user had some non-deterministic probability of being a non-user, and vice versa. In the case in which this exchangeability of comparison groups can be demonstrated, a necessary condition of interpreting the effect estimate as causal is achieved.
Conflict of Interest:
Response: "Hypnotics' association with mortality or cancer: a matched cohort study"
Dr. Daniel Kripke,
Thank you for you article entitled "Hypnotics' association with mortality or cancer: a matched cohort study," I enjoyed reading it and found it to be especially interesting. Nonetheless, I have a few comments and questions related to your research area and your article. Firstly, I thought the research design you choose was suitable for the nature of the research. The matched cohort study was sufficient in matching patients and controls based on age, gender, and smoking. However, there is no mention of how non-prescription drugs that may have been included within the sample population were accounted for. Also, how did you account for the incidence of people using these hypnotic drugs without a proper prescription? Additionally, I was wondering if the incidence of cancer and mortality could have been a result of the use of multiple medications by patients and their drug interactions. Furthermore, were any adjustments made for patients that could have had prior forms of cancer and how was it that the cancers studied developed within the 2.5 years. Secondly, I am interested in why only temazepam and zolpidem were presented in the data when any hypnotic user was noted in Table 1 of the results. What other drugs were reported in this study and why was not mention made of them and what were your inclusion criteria for which drugs were classified to fit into this study. Furthermore, you comment on temazepam being a benzodiazepine and the lethality being less severe than the drug class barbiturates. In saying this, there is evidence of there that supports that types of drugs in this class are not generally associated with a increased risk of cancer and mortality. Therefore, how can this increased risk of mortality and cancers be explained from your research? I also have a few concerns related to the statistical analyses of the data. I feel the lack of inclusion of other drugs and possible interactions warrant bias. I am also concerned the minimal information provided on the other drugs that were included in this study and the lack of cause of death that was reported. Finally, how were variables such as the socioeconomic status of your particular population taken into account and does this chosen group minimize the generalizaibility of this research (or rather introduce any form of selection bias). Overall, I found this article to be eye opening as these classes of drugs are commonly used. I think the research is a relevant topic as society is becoming increasing drug dependent ; however, I feel that more research needs to confirm these high rates of cancer and mortality. Randomized control trails would be ideal for this research in confirming these studies results. As always, research is just one piece of the puzzle, publicity and promotion of proper health practices are needed to ensure research like this becomes available to the public. Thanks for your article.
Re:Hypnotics and mortality: A time for action
We apologize if we created confusion by saying we "adjusted" for prior cancer. Indeed, our method of adjustment was to exclude all patients with any diagnosis of major cancer prior to the interval of observation. Similarly, when examining non-melanoma skin cancers, we excluded patients with prior skin cancers.
Unfortunately, only dichotomous responses concerning whether patients used alcohol were available in the data files utilized. That is a limitation of the study. A reliable quantitative history of alcohol use is sometimes difficult to obtain, but if it were available, it could have proven valuable in the analyses and could have reduced risks of residual biases.
It might be surprising that cancers of the lung, prostate, or colon would appear de novo within an average of 2.5 years, so the data may imply that an effect of hypnotics was to disinhibit the growth of pre-existing cancers, so that they were discovered. From a clinical point of view, what is important is not when microscopic cancers originate, but whether cancers reach a size and invasiveness that triggers clinical diagnosis and concern. Experimental evidence for the carcinogenic potential of hypnotics, which the manufacturers have not chosen to publish to my knowledge, may be found in internet files of the U.S. Food and Drug Administration New Drug Applications, and perhaps in similar European and international data sources. Those animal data do not indicate if the results reflect growth rates of cancers or their de novo neoplastic transformation.
Our manuscript cited four studies finding no association of insomnia with excess mortality, of which only one was authored by Dr. Kripke. The literature is complex and perhaps lacking in consensus, but there is consensus that the hazard ratio associated with insomnia is <2.0. Note that in our study, not all patients prescribed hypnotics received their prescriptions for a diagnosis of insomnia, and we have no reason to think that patients in the control group were free of insomnia. Because the contrast between those prescribed hypnotics vs. those not prescribed hypnotics was not a contrast of those with and without insomnia, and because the hazard ratio associated with insomnia is modest at best, insomnia could not explain much of the hazard ratio of 4.6 associated with hypnotic use.
We agree that cause of death data would be useful. However, that information is not recorded in the electronic health records that formed the basis for these analyses. We agree that osteoporosis should be prevalent in the older women in this cohort. However, it was necessary to restrict the classes of comorbidities which could be examined, and osteoporosis was one of many kinds of comorbidity which were not extracted from the electronic medical records.
With 18 previous studies showing an association of hypnotic use with mortality in addition to ours, and no studies suggesting that hypnotics prolong life or prevent cancer, the preponderance of evidence is now sufficient for clinical decisions. More independent studies will be valuable, but failing to act on available evidence now could cost lives.
Conflict of Interest:
Please see the parent publication.
Need for accessible non-drug treatmentsAs these distinguished authors write, efforts should be made to improve the accessibility of non-drug treatments for insomnia such as cognitive-behavioral approaches. By reducing the use of hypnotics, such treatments might be life-saving.
Conflict of Interest:
Please see our BMJ Open article
Insomnia in the UK: who cares?
Insomnia is twice as common in the UK as anxiety or depressive symptoms(1). Indeed, chronic insomnia is a risk factor for the development of such mental health problems(2). Yet in a week when new research shows that the prevalence of insomnia is increasing in England(3), and that even occasional hypnotic drug use continues to be associated with excess mortality(4), it is disappointing that after 21 months of waiting for a response, NICE has said that a broadly based call for the development of insomnia treatment guidance will not proceed through the topic selection process(5).
We see a parallel here to the situation 30 years ago, when leading researchers and clinicians denied the existence of obstructive sleep apnoea (OSA) in Britain(6). Fortunately, OSA is now widely and effectively treated in the NHS. What accounted for this remarkable transition? First, the adoption of OSA by the medical speciality of respiratory medicine; and second, the provision of NICE guidelines on treatment(7).
Insomnia likewise has lacked a clinical specialty to champion the disorder, but surely the recent development of psychological therapy services through the IAPT programme(8) offers the ideal opportunity for rational integration of pharmacological and cognitive behavioural treatments for insomnia in primary care? What is needed now is clear direction, by means of national guidelines, to structure clinical management and service provision in this neglected area. Otherwise, this opportunity will almost certainly be lost, with consequences measureable in degraded quality of life and amplified health risk among millions of patients(9).
We estimate that, over the past 15 years, the British public has supported over 5 million pounds worth of world-class research into the nature and optimal treatment of chronic insomnia; research that has greatly benefitted patients in other countries. To date, however, the British public has received a poor return on this investment and we trail far behind in the implementation of evidence-based practice. There can be few conditions where the discrepancy between what should be done, and what is being done, has been tolerated for so long.
1. Singleton N, Bumpstead R, O'Brien M, et al. Psychiatric morbidity among adults living in private households, 2000. London: The Office for National Statistics, HMSO;2001.
2. Baglioni C, Battagliese G, Feige B, et al. Insomnia as a predictor of depression: A meta-analytic evaluation of longitudinal epidemiological studies. J Affect Disord 2011;135:10-19.
3. Calem M et al. Increased Prevalence of Insomnia and Changes in Hypnotics Use in England over 15 Years: Analysis of the 1993, 2000, and 2007 National Psychiatric Morbidity Surveys. Sleep 2012;35(3):377-384
4. Kripke DF, Langer RD, Kline LE. Hypnotics' association with mortality or cancer: a matched cohort study. BMJ Open 2012;2:e000850. doi:10.1136/bmjopen-2012-000850
5. NICE Topic Selection Team. Personal communication. 8 Feb 2012.
6. Shapiro CM, Catterrall JR, Oswald I, Flenley DC. Where are the British sleep apnoea patients?. Lancet 1981; ii: 523.
7. National Institute for Health and Clinical Excellence (NICE). Technology Appraisal Guidance 139: Sleep apnoea - continuous positive airway pressure (CPAP), NICE, 2008.
8. Department of Health. IAPT Programme Review December 2011 v2.2. http://www.iapt.nhs.uk/silo/files/iapt-programme-review-december.pdf (accessed 3 March 2012)
9. Mental Health Foundation (MHF). Sleep Matters: The impact of sleep on health and wellbeing. London, MHF 2011.
Colin Espie, Professor of Clinical Psychology, University of Glasgow; Director, University of Glasgow Sleep Centre
Kevin Morgan, Professor of Gerontology, Loughborough University; Director, Clinical Sleep Research Unit, Loughborough University
David Nutt, Professor of Neuropsychopharmacology, Imperial College London
Niroshan Siriwardena, Professor of Primary and Prehospital Health Care, University of Lincoln
Derk-Jan Dijk, Professor of Sleep and Physiology, University of Surrey; Director, Surrey Sleep Research Centre
Brian McKinstry, Professor of Primary Care E-Health, University of Edinburgh
June Brown, Senior Lecturer in Clinical Psychology; Joint Head of Mood, Anxiety and Personality (MAP) Clinical Academic Group (CAG), South London & Maudsley NHS Foundation Trust
John Cape, Head of Clinical Psychology, Camden & Islington NHS Foundation Trust, London
Sue Wilson, Senior Research Fellow, University of Bristol; President, Sleep Section, Royal Society of Medicine
Maureen Tomeny, Consultant Clinical Psychologist, Clinical Director of IAPT Services, Nottinghamshire Healthcare NHS Trust
Andrew McCulloch, Chief Executive, Mental Health Foundation, London
Neil Douglas, Professor of Sleep & Respiratory Medicine, University of Edinburgh; Chairman, Academy of Medical Royal Colleges, UK
Conflict of Interest:
Hypnotics and mortality: more evidence is needed
We have read with great interest the recent article by Kripke DF, Langer RD and Kline LE that assessed the risk of all cause mortality and cancer incidence in patients using benzodiazepines or zolpidem. The article poses relevant questions about the use of these drugs and it is likely to have a very large influence on the decisions that health care practioners take, particularly because of the large number of patients studied, the magnitude of the HR found and the fact that there are few articles examining a possible relation between hypnotics and mortality. However, our attention was drawn to some possible limitations that might make the interpretation of the results difficult on a daily basis.
The first issue that we noticed was that in the abstract and in the supplementary files Kripke DF et al state that the stratified models were adjusted for prior cancer, while on the methods section it is explicitly stated that patients with prior cancer (other that non-melanoma skin cancer) were excluded from the study. We could not find any adjustement for prior cancer in any table in the published article, or in supplementary table 7. This might lead to some confusion as it is not clear if the Cox proportional hazard model was indeed adjusted for prior cancer, and it could pose a limitation to the external validity as insomnia is more prevalent in cancer patients .
We also noticed some problems in the design regarding covariates used for adjustement. Alcohol use was classified as a dichotomous variable, depending on the patient's self response to alcohol use in a yes or no question. This could pose an important limitation to the study, as alcohol is a recognized dose dependant depressant in the central nervous system acting as an agonist in GABA receptors and it might act synergistically with benzodiazepines to induce sedation. The alcohol related central nervous system depression is not equivalent between low alcohol consumption and high alcohol consumption, and we believe that alcohol use should have been an ordinal variable in the Cox proportional hazards model used. According to supplementary table 3, there was a significant prevalence (between 35-45%) of alcohol use in hypnotic users, and since the quantity of alcohol was not taken into consideration there might have been important differences between the hypnotic users and the control group that could influence the results introducing selection bias.
Kripe et al analyzed the HR for incident cancers in hypnotic users compared with non users, and it was statistically significant for some important cancers like lymphoma, colon cancer and lung cancer. This is very important for clinical practice, as doctors and patients might not know about a possible carcinogenetic effect of hypnotics and might consider alternative therapies if the results obtained by Kripke et al are consistent with further studies. Nevertheless, we find the results difficult to interpret in relation with lung, prostate and colon cancer. The mean follow up of this cohort study was 2.5 years, and it is widely known than lung, prostate and colon cancer take many years to develop. We are skeptical as to whether the incident cancers are indeed related to hypnotic use, as it is plausible that hypnotic users had an undiagnosed cancer before hypnotic prescription, and developed cancer independently of hypnotic use. Furthermore, since hypnotic users differed from the non users on insomnia and sleep related problems they might have been more carefully examined in hospital visits, leading to selective overdiagnosis. This is particularly relevant to prostate cancer and to lung cancer . The temporal sequence between hypnotics and cancer has not been assessed robustly, and further studies should have a longer follow up of participants to analyze this relation as it is possible that an undiagnosed cancer lead to insomnia and hypnotic use and not the other way around as Kripke et al discuss in their article. To our knowledge, there is no experimental evidence for the carcinogenetic potential of hypnotics except a previous study by Kripke DF. It would be more prudent to wait for studies done by other researchers in order to see if the results are consistent.
Perhaps the main factor that makes it difficult to interpret the results is that the cause of death was not reported. This fact was taken into consideration in the article's discussion, where Kripke et al cite articles that suggest many pathways by which hypnotics may lead to excess mortality. It is true that hypnotic use leads to impared balance and cognition, and that there are numerous articles that find an association between hypnotic use and adverse health outcomes but it is also true that insomnia is associated with an increase in mortality , . Kripe et al states that several large studies have found that insomnia is not a significant mortality favor, but we could retrieve few articles by independent researchers that support the statement. In fact, most of the articles that support the statement are written by Kripe et al . We are concerned that a confirmation bias might be present in this article, as the relationship between insomnia and mortality was dismissed, but there is sufficient evidence that insomnia is associated with an increase in mortality. It could be that the increase in mortality was not due to hypnotics but to insomnia, so the effect would be independent of hypnotic use or even decreased by hypnotic use. Besides, there are other comorbilities that ought to have been included as coviarates. We find that osteoporosis and prior fracture history might be relevant in geriatric patients, as there are various well designed studies that show an increased mortality risk in geriatric patients after fractures . Since more than 60% of the population in the cohort are women, osteoporosis should have been taken into consideration and failure to account for different prevalence between the hypnotic users and non users could limit the applicability of the results.
In conclusion, the available evidence of an association between hypnotics and mortality is not sufficiently vigorous. There are many coviarates that might have introduced selection bias, so the specific contribution of hypnotics to mortality is difficult to determine objectively. The possibility of overdiagnosis of cancer, and of residual confounding due to indication is still present in the study. More independent studies are needed assessing the possible risks of benzodiazepines in order to give health care recommendations. We consider that it would be prudent to wait for more evidence before condemning hypnotics.
1 Kripke DF, Langer RD, Kline LE. Hypnotics' association with mortality or cancer: a matched cohort study. BMJ Open 2012;2:e000850. doi:10.1136/bmjopen-2012-000850
2 Palesh OG, Roscoe JA, Mustian KM, Roth T, Savard J, Ancoli-Israel S, Heckler C et al. Prevalence, Demographics, and Psychological Associations of Sleep Disruption in Patients With Cancer: University of Rochester Cancer Center-Community Clinical Oncology Program. Journal of Clinical Oncology. 2010; 10;28(2):292-8.
3 Ashton H. Toxicity and adverse consequences of benzodiazepine use. Psychiatric Annals. 1995;25:158-65.
4 Longo L, Johnson B. Addiction: Part I. Benzodiazepines- Side effects, Abuse Risk and Alternatives. Am Fam Physician. 2000; 1.61(7):2121 -28
5 U.S. Preventive Services Task Force. Screening for Prostate Cancer: U.S. Preventive Services Task Force Recommendation Statement. Annals of Internal Medicine. 2008; 149.3: 185-91
6 Marcus PM, Bergstralh EJ, Fagerstrom RM, Williams DE, Fontana R, Taylor WF, Prorok PC. Lung cancer mortality in the Mayo Lung Project: impact of extended follow-up. J Natl Cancer Inst.2000; 92 (16): 1308-16
7 Vgontzas A, Liao D, Pejovic S, Calhoun S, Karataraki M, Basta M et al. Insomnia with Short Sleep Duration and Mortality: The Penn State Cohort. Sleep.2010; 33(9): 1159-1164
8 Prospective Study of the Association between Sleep-Disordered Breathing and Hypertension Peppard PE, Young T, Palta M, Skatrud J. Prospective Study of the Association between Sleep- Disordered Breathing and Hypertension. New England Journal of Medicine. 2000; 342: 1378-84
9 Kripke DF, Garfinkel L, Wingard D, Klauber M, Marler M. Mortality associated with sleep duration and insomnia. Arch Gen Psychiatry. 2002; 59: 131-36
10 Bliuc D, Nguyen N, Milch V, Nguyen T, Einsman J, Jacqueline R. Center. Mortality Risk Associated With Low-Trauma Osteoporotic Fracture and Subsequent Fracture in Men and Women. JAMA. 2009; 301(5):513-21
Conflict of Interest:
Why weren't people with insomnia who didn't take hypnotics included in the control group-could insomnia and not hypnotics be the factor causing excess death???Is the dose relationship just an indication of the severity of insomnia?
Conflict of Interest: