|
Psychiatric Drugs |
|
Psychiatric drugs increase mortality rate by 350%
Major
matching study controlled for contravening variables) confirms that
anxiety drugs and by extension nearly all neuroleptic drugs (better termed
“downers” or “tranquilizers” greatly increase risk of dying (3.5 fold
increase). Downers are pharma’s wet
dream, for most patients then become much more susceptible to their doctor’s
recommendations for additional drugs. Downers
find a myriad of uses besides for psychiatric treatments, such as muscle
relaxants, anticonvulsants, blood pressure meds, anti-nauseous, menstrual and
menopause indications, and for chronic pain.
The only major exception I know to this is the SSRI Wellbutrin, which
actually is a mood elevator. “The age-adjusted hazard ratio (HR) for mortality was 3.46
(95% confidence interval [CI], 3.34 - 3.59) for the patients who used any of
the study drugs during the first year after baseline compared with those who
did not take any of the drugs. After
further adjusting for potential confounders, the HR for mortality for this
group was still 3.32 (95% CI, 3.19 - 3.45)” Medscape. “Evidence
of adverse effects5 including
increased risk of dementia6 7 8 and other
psychomotor impairments
(daytime fatigue, ataxia, falls, and road traffic incidents),910 11 12 13 14 cancer,15 16 17 pneumonia,
and other infections18 has increased
concerns of an
association with premature mortality. Considering that
many of those in the study were off neuroleptic drugs, this high rate is worse
than if they included only patients who were on psychiatric drugs for the
entire period of follow-up” BMJ below. Though pharma argues that newer drugs are
better,
quality studies have failed to uncover a significant difference. Over
and over again the sham of psychiatric downers are exposed, but pharma, the $600
billion gorilla, owns their clinical trials, controls prescribing practices through
guidelines, physicians belief through their opinion leaders, and patient
beliefs through corporate media.
Negative findings such as this one are buried in an information blitz that
repeats their mantra of safe and effective.
Neuroleptic
drugs exacerbate
psychiatric conditions has been convincing proven in a number of studies. Based
on breaking blind, the positive
bias in journal articles must be significantly greater than the 32% uncovered in a
study using the raw data compared to the journal articles. Breaking blind occurs
when either the patient
or the physician comes to a belief as to which group the patient is in, the
placebo or treated; it occurs correctly over 80% of the time for both the
patient and the physician. See Irving
Kirsch, The Emperor’s New Drugs:
Exploding the Antidepressant Myth, Basic Books, 2010.
Definitions
Neuroleptic,
capable of affecting the brain, especially by reducing intensity of nerve
function; tranquilizing. A major
tranquilizer used to treat psychiatric conditions.
Anxiolytic,
anxiety relieving,
anti-anxiety drug.
Hypnotic
drug, soporific drug
(producing sleep), producing sedation; in street usage a downer.
Pharma is very good at
finding other uses for these drugs with the help
of a pro-pharma FDA and its low hurdle of better than a sugar pill. BMJ 2014; 348 doi: http://dx.doi.org/10.1136/bmj.g1996 (Published 19 March 2014), Cite this
as: BMJ 2014;348:g1996 Effect of anxiolytic and hypnotic drug
prescriptions on mortality hazards: retrospective cohort study Objective To
test
the hypothesis that people taking anxiolytic and hypnotic drugs are at
increased risk of premature mortality, using primary care prescription records
and after adjusting for a wide range of potential confounders. Design Retrospective
cohort study. Setting 273
UK
primary care practices contributing data to the General Practice Research
Database. Participants 34 727
patients aged 16 years and older first prescribed anxiolytic or hypnotic drugs,
or both, between 1998 and 2001, and 69 418 patients with no prescriptions for
such drugs (controls) matched by age, sex, and practice. Patients were
followed-up for a mean of 7.6 years (range 0.1-13.4 years). Main outcome All
cause mortality ascertained from practice records. Results Physical
and psychiatric comorbidities and prescribing of non-study drugs were
significantly more prevalent among those prescribed study drugs than among
controls. The age adjusted hazard ratio
for mortality during the whole follow-up period for use of any study drug in
the first year after recruitment was 3.46 (95% confidence interval
3.34 to 3.59) and 3.32 (3.19 to 3.45) after adjusting for other potential
confounders. Dose-response associations were found for all three classes of
study drugs (benzodiazepines, Z drugs (zaleplon, zolpidem, and zopiclone), and
other drugs). After excluding deaths
in the first year,
there were approximately four excess deaths linked to drug use per 100 people
followed for an average of 7.6 years after their first prescription. [They should have used all causes of
death,
not merely those which could be ascribed to the drug. Many deaths, such as increased
rate from
heart attack could well be greater in the treated group but not considered
caused by the medication (“linked to
drug use”),] Conclusions In
this
large cohort of patients attending UK primary care, anxiolytic and hypnotic
drugs were associated with significantly increased risk of mortality over a
seven year period, after adjusting for a range of potential confounders. As
with all observational findings, however, these results are prone to bias arising
from unmeasured and residual confounding. Prescribing of hypnotic and anxiolytic drugs is common1 and increasing in places.2 In 2011-12 more than 16 million prescriptions
for these drugs3 were written in general practice in England
at a cost of over £60m ($100m; €73m) per annum. Benzodiazepines currently
account for 62% and Z drugs (zaleplon, zolpidem, and zopiclone) 32% of total
prescriptions for hypnotics and anxiolytics in primary care in England.2 4 Evidence of adverse effects5 including increased risk of dementia6 7 8 and other psychomotor impairments (daytime
fatigue, ataxia, falls, and road traffic incidents),910 11 12 13 14 cancer,15 16 17 pneumonia, and other infections18 has increased concerns of an association
with premature mortality. Until recently evidence for this was based on a small
number of studies, which varied in setting, sample (especially age
distribution), length of follow-up, source of drug usage data,19 20 21 type of drug, and the extent of control for
confounding (especially from physical and psychiatric comorbidity,
co-prescribing, socioeconomic status, smoking, and drug and alcohol misuse).7 22 23 Although two studies in older populations
did not report a statistically significant association between benzodiazepine
use and mortality after adjusting for confounders,24 25 four others (in younger samples) found
evidence of significantly increased mortality.19 20 2223 26 A study in people with schizophrenia
reported associations with suicide and with all cause mortality.27 Adjusted hazard ratios have varied
substantially, ranging from 1.1421 to 4.56.16 23 27 A recent study23 found that the mortality risk extended to
those with low levels of use, was greater in younger people, and that heavy use
of hypnotics increased the risk of developing cancer.23 Questions remain about effect size,
interactions with age,20 22 24 25 and confounding (particularly by anxiety
and other psychiatric disorders). We tested the hypothesis that
people taking anxiolytic or hypnotic drugs, or both, are at significantly
increased risk of death compared with non-users and to estimate the size of
this association after adjusting for a wide range of potential confounders
using prescribing data from UK primary care. We undertook a retrospective, matched cohort study using the
General Practice Research Database (GPRD). GPRD (incorporated into the Clinical
Practice Research Datalink in 2012) was created in 1987 and is the largest
anonymised, longitudinal primary care database in the world, with around 70
million patient years of high quality validated data from 630 practices. In
2011 over 11 million patient records were in the GPRD (five million active),
equivalent to 8.3% of the UK population.28 The database contains records from clinical
consultations with general practitioners, prescriptions, secondary care
referrals, and hospital admissions. This project was awarded a
licence as part of a scheme operated by the UK Medical Research Council and
Medicines and Healthcare products Regulatory Agency to provide data access on
up to 100 000 patients. Data were based on records from 273 primary care
practices in England, Scotland, Wales, and Northern Ireland. Eligible participants were patients aged 16 years and older,
permanently registered with a practice contributing data to the GPRD, and with
at least 12 months of up to standard records (as per GPRD data quality
standards). We identified patients who had received study drugs by incident
(first ever) prescription of an anxiolytic or hypnotic drug (see chapters 4.1.1
and 4.1.2 of the British
National Formulary29),
excluding barbiturates, during the recruitment window from January 1998 to
December 2001. We only included patients who received at least two
prescriptions for a given study drug during the recruitment period. This was
done to minimise misclassification of use among people who received but did not
fill the prescription or take the drug.30 31 We reasoned that a second (that is, repeat)
prescription indicated that the first had been filled and taken. Examination of
a subsample of GPRD records (not reported here) found that 40.3% of people in
receipt of a lifetime prescription for an anxiolytic or hypnotic drug only ever
received a single prescription for that drug. No prescriptions for any study
drugs were recorded for participants (whether users or non-users) for the
duration of their practice record before recruitment into the study. Mean
duration of registration with study practices before recruitment was 15.6 years
(SD 14.0). To improve efficiency and
reduce the number of required patients who were prescribed the study drugs, we
matched each patient prescribed any study drugs to two controls from among
those with no prescription for any study drugs, on age (three years either
way), sex, and practice. The 2:1 recruitment strategy was also determined by
the 100 000 limit on the total sample size under the terms of our data license.
Matching occurred (and follow-up started) at the time of the first prescription
for a study drug. The period during which the study outcome (death) was ascertained
therefore began at exactly the same time for both patients prescribed the study
drugs and (matched) controls. Both groups of patients were followed until the
earliest of death, censorship (no longer registered with practice), or
truncation (end of the observation period on 31 October 2011). Study outcome was
all cause mortality as
recorded in the practice record. The observation period for the ascertainment
of covariates was the entire interval for which data are available for a
patient between the time their record starts (before recruitment) and either
death, censorship, or truncation. To reduce the likelihood of bias arising
from the prescription of study drugs to those who were terminally ill and
nearing the end of life, we restricted the study sample further in our final
model to patients who survived for longer than 12 months after recruitment. We ascertained the receipt of hypnotic and anxiolytic drugs from
electronic prescribing records. Use was initially quantified in terms of
defined daily doses from study entry point to the end of each patient’s
observation period. The defined daily dose is the assumed average maintenance
dose per day for a drug used for its main indication in adults (considered to
be someone of 70 kg body weight).32 The defined daily dose, a measure of
equivalence that permits pooling of usage data across different drugs used for
the same indications and values, are available from the WHO Collaborating
Centre for Drug Statistics Methodology (www.whocc.no/atc_ddd_index). The
defined daily doses in the exposed group were recoded as a categorical
variable: 1-30, 31-60, 61-90, and ≥91, corresponding to prescriptions of one,
two, three, or more than three months’ duration. We classified study drugs as
benzodiazepines, Z drugs (zaleplon, zolpidem, and zopiclone), and other.
Patients who were prescribed study drugs were further dichotomised according to
whether or not the study drug continued to be prescribed after the first 12
months of observation. Statistical adjustment was
undertaken for potential confounders. Controlling for confounding by indication
(that is, possible reasons for being prescribed a study drug) is especially
important. Potential confounders included sex, age at study entry, sleep
disorders, anxiety disorders, other psychiatric disorders, medical morbidity,
and prescriptions for non-study drugs. Smoking and alcohol use were recorded
within the dataset as current, former, or never. As a means of controlling
partially for differences in socioeconomic status, we matched patients who were
or were not prescribed study drugs by practice. Medical morbidity was ascertained using Read codes for arthritis
and musculoskeletal problems, asthma, cancer, chronic obstructive pulmonary
disease, diabetes, gastrointestinal disorders, epilepsy, hypertension,
ischaemic heart disease, stroke, and sleep disorders (www.connectingforhealth.nhs.uk/systemsandservices/data/uktc/readcodes). We
subdivided psychiatric codes into anxiety disorders (the main indication for anxiolytic
prescribing) and all other psychiatric disorders. Using Cox proportional hazards
models, we estimated the hazard ratios for death after recruitment into the
study cohort (defined as the first prescription of a study drug). Exploratory
analyses showed that the hazard function (for the association between study
drugs and mortality) varied with age (results available from authors); we
therefore stratified regression analyses by this variable. In the first model we included
prescriptions for all study drugs during the observation period (following
recruitment) and included all deaths, regardless of timing. In the second model
(to minimise confounding of use by survival) we restricted the exposed patient
sample to those who were prescribed study drugs only in the first year after
recruitment. All deaths were included, regardless of timing. In the third and
final model, we further restricted both patient groups to those who survived
for more than 12 months (and therefore after study drug prescription had ceased
in the group using the study drugs). We assessed the extent of
co-prescribing of study drugs. Since 75.9% (n=26 347) of patients who used
study drugs had received at least one prescription for a benzodiazepine and
31.5% (n=10 877) had received more than one class of study drug, we opted to
pool estimates of association with mortality across groups in our primary
analyses. We undertook subgroup analyses in which the group prescribed the
study drugs was restricted to those who received benzodiazepines only, Z drugs
only, or other study drugs only, in the first year after recruitment. MF and HP
undertook all analyses by using SPSS version 19.0. Data were obtained on 34 804 patients who were prescribed the
study drugs and 69 585 patients (matched) who were not (controls). Seventy
seven patients who were prescribed the study drugs were excluded (with 154
matched controls) owing to insufficient data to allow defined daily doses to be
calculated. We also excluded 13 “unexposed” patients who had been prescribed
melatonin during the observation period. The final sample for study models
comprised 104 145 patients, of whom 34 727 were prescribed the study drugs and
69 418 were controls. Censorship (excluding death) was observed for 26.7%
(n=9314) of the patients who were prescribed the study drugs and 31.2%
(n=21 644) of controls (table 1⇓). View
this table: Table 1 Study
drugs by drug class, showing defined daily doses (DDDs) and proportion of
patients (n=34 727) who received a prescription for each of these during the
observation period Benzodiazepines (63.7% (n=22 116) of patients prescribed the
study drugs) were more common as the index drug class than Z drugs (23.0%)
(n=7971) or other study drugs (13.4%) (n=4640). Co-prescribing was common
(table 2⇓). In total, 76.3% (n=26 436)
of patients using study drugs
received a prescription for a benzodiazepine, 38.8% (n=13 444) a prescription
for a Z drug, and 33.5% (n=7444) a prescription for one or more of the other
study drugs. The most commonly prescribed study drugs were diazepam (47.9% of
those prescribed the study drugs, n=16 638), temazepam (35.1%, n=12 208), and
zopiclone (34.1%, n=11 764). Among the group prescribed the study drugs, 24.2%
(n=8404) were only prescribed diazepam, 14.8% (n=5140) only temazepam, and
12.2% (n=4237) only zopiclone. Table 2 Patterns
of prescribing and co-prescribing of study drugs at any time during observation
period Table 3⇓ shows
the characteristics of the study sample. Patients who were prescribed study
drugs were more likely than controls to be current smokers and to have higher
rates of all forms of physical morbidity, most notably cancer and respiratory
disorders. The group prescribed study drugs also had higher rates of sleep
(28.1% (n=9741) v 5.8% (n=4009)), anxiety (44.1% (n=15 299) v 11.3% (n=7849), and other psychiatric
disorders (56.9% (n=19 770) v 21.7% (n=15 026)) than controls,
and
received more prescriptions for non-study drugs. View
this table: Table 3 Characteristics
of participants by use of study drugs. Values are percentages (numbers) unless
stated otherwise We found statistically significant associations with mortality
at all levels of study drug use. Our initial model classified use irrespective
of when this occurred, and included all deaths regardless of when these
occurred during the observation period (table 4⇓). The hazard ratio for mortality
in the group with the highest
use of study drugs was lower than that in all three groups with fewer defined
daily doses, suggesting that use was confounded by survival. We also noted
reverse confounding on adjusting for study covariates. View
this table: Table 4 Hazard
ratios (95% confidence intervals) for age adjusted associations between defined
daily doses (DDDs) of study drug (versus no study drugs) before and after
adjusting for other potential confounders In the second model (table 5⇓), the exposed group was restricted
to those who received no
prescriptions for the study drugs after their first year of observation. The
age adjusted hazard ratio for mortality for any use of study drug was 3.46 (95%
confidence interval 3.34 to 3.59), decreasing slightly to 3.32 (3.19 to 3.45)
after adjusting for potential confounders. A clear dose-response association
was found, with an adjusted hazard ratio for mortality of 4.51 (4.22 to 4.82)
among those who received more than 90 defined daily doses of any study drug in
the first year of follow-up. Associations with mortality, and dose-response
effects, were found for each of the three separate classes of study drug.
Hazard ratios were largest for benzodiazepines and smallest for other study
drugs (table 5). View
this table: Table 5 Hazard
ratios (95% confidence interval) for age adjusted associations between defined
daily doses (DDDs) of study drug (versus no study drugs) and mortality before
and after adjusting for other potential confounders*, for exposure restricted
to receipt of study drugs in first year after recruitment only We further excluded patients in both groups with less than one
year of follow-up (model 3, table 6⇓). Those who survived the first year
but did not receive
prescriptions for the study drugs beyond the first year of observation are the
subgroup analysed in table 6. They had lower rates of physical and mental
health problems on all 14 indicators of comorbidity than those who were
prescribed study drugs beyond the first year, including cancer (22.9% (n=5050) v 18.6% (n=1599)), chronic obstructive
pulmonary disease (15.7% (n=3449) v 13.5% (n=1158)), and ischaemic heart
disease (22.5% (n=4955) v 19.6% (n=1683)). Those only prescribed
study drugs in year 1 also differed slightly from those who took study drugs
beyond the first year on mean age at study entry (52.6 years (SD 18.9) v 54.3 years (SD 18.6), P<0.001) and age
at death (77.2 years (SD 13.8) v 76.8 years (SD 14.3), P=0.38). Patients
who
were only prescribed study drugs in year 1 were less likely to die than those
who continued to take drugs (18.8% (n=1610) v 22.0% (n=4852)) but more likely to be
censored for other reasons (33.5% (n=3028) v 22.3% (n=4906)). View
this table: Table 6 Hazard
ratios (95% confidence intervals) for age adjusted associations between defined
daily doses (DDDs) of study drug and mortality before and after adjusting for
other potential confounders, for exposure restricted to receipt of study drugs
in first year after recruitment only and for patients with at least 12 months
of follow-up Patterns of association
remained in this third model, although effect sizes were reduced (adjusted
hazard ratio for >90 defined daily doses was reduced to 2.63 (95% confidence
interval 2.34 to 2.95), table 6). The same patterns of association were found
across all three classes of study drugs, with hazard ratios for benzodiazepines
being the largest. The adjusted hazard ratio for use of any drug in model 2
(table 5), which included early deaths during drug use, was 3.32 (95%
confidence interval 3.19 to 3.45), compared with an adjusted hazard ratio for
any drug use in model 3, limited to deaths after prescriptions for the study
drugs had finished, of 1.75 (1.65 to 1.85, table 6). We found evidence of an
association between prescription of anxiolytic and hypnotic drugs and mortality
over an average follow-up period of 7.6 years among more than 100 000 age and
general practice matched adults. In patients who were prescribed these drugs, there
was an estimated overall
statistically significant doubling of the hazard of death (hazard ratio 2.08),
after adjusting for a wide range of potential confounders, including physical
and psychiatric comorbidities, sleep disorders, and other drugs. [This
adjustment is flawed because psychiatric drugs are causal factors for weight
gain, suicide, sleep disorder, drug interaction, and metabolic syndrome, and
thus all causes should be included which gives us a 3.46 hazard ratio.] This
association remained significant and followed a dose-response pattern after
restricting analyses to those with at least 12 months of follow-up and to those
who were only prescribed the study drugs in the first year after recruitment
(hazard ratio 1.75). Crude cumulative mortality in those given drugs was 26.46
per 100 people over the full follow-up period compared with 16.82 per 100
controls. After excluding deaths in the first year, there were approximately
four excess deaths linked to drug use per 100 people followed for an average of
7.6 years after their first prescription. While overall effect sizes were broadly in keeping with most
previous findings, our estimates of association were lower than that reported
by one study,23 which reported an adjusted hazard ratio of
4.56 over 2.5 years. This may reflect differences in the length of follow-up,
as both studies reported declining associations with mortality over time. Use of data from the UK General Practice Research Database was
an obvious strength, given the size and representativeness of the sample, and
the quality, completeness, and duration of the follow-up data. Data on drug use
were based on documented prescriptions rather than self reported receipt or use
of drugs. We had detailed information on a wide range of potential confounders,
going back several years. In particular, we were able to control for a large
number of physical and psychiatric morbidities as well as prescriptions of
other drugs. This is especially important given the possibility of confounding
by indication (that is, study drugs may be given more often to those who are
seriously ill and who may not be able to sleep because of pain or other
consequences of long term or life threatening illnesses). In contrast with a
recent report,23 we were able to adjust for anxiety
disorders as well as all other psychiatric disorders. We were also able to
identify and control for recorded instances of sleep problems (including those
secondary to physical and psychiatric disorders). Our recruitment strategy and ascertainment of drug use were
further strengths. We minimised misclassification by excluding people who had
received only one prescription, since some people never fill prescriptions or
take the drugs. Using defined daily doses to quantify cumulative use of study
drugs allowed us to combine the effects of different drugs in a way that is not
possible by counting prescriptions or pills.23 In further contrast with previous research,23 we chose to classify study drugs by class
rather than by indication for the purposes of recruitment; for example, we
included all benzodiazepines, not just those recorded as having been prescribed
for insomnia. We would argue that this resulted in a more accurate estimation
of use of these drugs, as well as ensuring that our results are generalisable
to all of those who receive anxiolytic and hypnotic drugs in primary care. Our
models were adjusted for all main indications for these drugs. Although pooling
of study drugs may have overlooked variation in associations with mortality
across classes, subgroup analyses indicated statistically significant
associations (and dose-response effects) between mortality and all three
classes of study drug. The largest hazard ratios were found for
benzodiazepines. Despite using prescribing records, we may have underestimated
use of study drugs. Patients with more serious psychiatric disorders may be
cared for by secondary care services rather than solely in primary care.
Although in most cases responsibility for longer term (repeat) prescribing is
usually delegated to general practice, it is possible that prescribing for
these patients may be under-recorded in the General Practice Research Database.
Likewise, we had no information on the use of study drugs that were obtained
illicitly, although this was likely to have been modest compared with use of
prescribed drugs. It is highly unlikely that study drugs were used before
recruitment among the patients eventually prescribed the drugs or controls,
given that the patients were registered with the study practices for 15 years
on average. This was not so in a previous study,23 in which around one fifth of the exposed
group had received a prescription for a study drug before recruitment. The length of follow-up was
also a strength, particularly for the generalisability of the findings.
However, higher effect estimates obtained when we restricted our sample of
exposed patients to those with no further prescriptions for the study drugs
after the first 12 months suggests that results from our initial model, which
included patients who continued to receive prescriptions for the study drugs
throughout the observation period, may have been biased towards the null by the
confounding of use and survival. Results of models in which use was restricted
to the first year after recruitment and deaths restricted to those occurring
after that first year suggest that much of the excess mortality risk arises
early in the period of drug use but remains statistically significant even
after discontinuing study drugs. We were not, however, able to explore temporal
risk trajectories in detail. It was possible that patients who discontinued
drugs within the first year did so because they were particularly unwell (and
more morbid than those who continued to take these drugs). However, our
findings show that the opposite was true, which strengthens the validity of our
estimates of excess mortality in this group compared with the control group.
Although those for whom prescriptions for study drugs stopped after the first
year were more likely to be censored for reasons other than death, there is no
reason to believe that this inflated the association between study drugs and
mortality. Non-randomised outcome studies are especially prone to
confounding, including confounding by indication. One option for dealing with
confounding by indication is using a comparator group more closely aligned with
the exposed group—for example, patients who were starting other types of drugs.
However, in the absence of previous evidence that comparator drugs were free of
other indication effects, this would again have not ruled out this bias, even
though it may have accounted for bias related to the comparison with non-users.
Instead, we chose to deal with this in four ways: by taking account of a large
number of potential confounders, by comparing effects across different groups
of study drugs, by conducting subgroup analyses that limited exposure to year 1
and excluded all deaths during that first year in patients who both used and
did not use the study drugs (on the grounds that confounding by indication will
have the largest effect in year 1), and by adjusting our estimates of
association for comorbidities occurring across the entire follow-up period.
Nevertheless, although we controlled for many potential factors that were
associated with study drug use and mortality and eliminated confounding of use
and survival, it is impossible to exclude confounding arising from unmeasured
factors or measurement error.33 34 35 While effects on estimates of association
can be substantial,33 such bias is greatest for unmeasured
confounders and those that are uncorrelated with other confounders but
correlated with the study exposure.34Bias
tends to be greatest in studies that control for relatively few measured
confounders.34 Although bias due to confounding was likely to have occurred, the
impact was offset by the large number of covariates included in our analyses.
One important unmeasured confounder is socioeconomic status, since records in
the General Practice Research Database do not include detailed information on
occupation, education, housing tenure, income, or employment. However, this
variable was partially controlled for by matching by practice. Residual
confounding, arising from a mixture of misclassification and indication, was
also likely to have occurred in the recording of clinical diagnoses, and
through our inability to quantify the severity of illness. Again, this is
likely to have been offset to an extent by controlling for a wide range of
comorbidities. Adjustment for a large number of measured confounders failed to
negate our finding of an association between drug use and mortality but has
resulted in appropriately more conservative estimates of the size of this
association.23 Cohort studies are also prone to immortal time bias, which
arises if the period participants are considered at risk differs between
comparator groups.36 Although mortality was counted from the
time of the first prescription for all patients, the time until second
prescription would be “immortal” for patients who used the study drugs and who
had to survive to get a second prescription to be in the study. This would not
have applied to controls. However, excluding deaths among those who did not
survive to receive a second prescription would have underestimated mortality in
patients who used the study drugs. Any bias in the mortality comparison would
therefore have been towards the null. Furthermore, this would not have biased
the subgroup analysis that excluded early deaths, since deaths were ascertained
only after the first year of follow-up for patients who both did and did not
use the study drugs. We considered the possibility of collider bias, a form of
selection bias that may occur when two variables are not associated but share a
common antecedent or outcome. Adjusting for such a factor can result in a
spurious association.37 It is possible, for example, that study
drug use and mortality are both associated with (for example) physical illness
but themselves are not related. Since adjusting for comorbidities reduced
estimates of association between study drugs and mortality, we suggest that
these variables were likely to have been acting as classic confounders rather
than sources of selection bias. We did not have access to data
on cause of death and therefore were unable to explore associations between
prescription of study drugs and specific forms of morbidity such as pneumonia.
Neither did we explore interactions between individual forms of morbidity and
vulnerability to specific drug classes. In the light of consistent evidence of
associations with mortality, such investigations are needed and will be the
subject of future studies. These findings are consistent
with previous evidence of a statistically and clinically significant
association between anxiolytic and hypnotic drugs and mortality. Using
prescribing data from a large primary care database and after adjusting for a
wide range of potential confounders, prescriptions for these drugs were
associated with significantly increased risks of mortality over an average
follow-up period of 7.6 years. This association followed a dose-response
pattern for all three classes of study drug and extended beyond the time of
use. However, as with all observational studies, these findings remain prone to
many forms of bias. While we have largely excluded immortal time bias and
selection bias, we are unable to exclude the possibility that the results were
due to confounding by indication or to residual confounding by unmeasured or
incompletely measured factors, such as socioeconomic status. This applies
especially to deaths in the first year of observation. These results add to
evidence of an association with mortality, but must be treated with caution. Anxiolytic and hypnotic drugs are addictive and associated with
cognitive and psychomotor impairments, falls, and unintentional injuries It has long been suspected that these drugs are associated
with
premature mortality Studies of the association between anxiolytic and hypnotic drugs
and mortality have reported widely varying effect sizes, reflecting variation
in methods In this large cohort of patients attending UK primary care,
anxiolytic and hypnotic drugs were associated with a significantly increased
risk of mortality over a seven year period After excluding deaths in the first year, there were about four
excess deaths linked to drug use per 100 people followed for an average of 7.6
years after their first prescription The risk followed a dose-response pattern and was found for all
three classes of study drugs and did not seem to be entirely due to confounding
by physical or psychiatric comorbidity or prescribing of other drugs This study controlled for a wide range of potential confounders
including the major sources of confounding by indication Cite this as: BMJ 2014;348:g1996 This study is based on data from the Full Feature General
Practice Research Database obtained under licence from the UK Medicines and
Healthcare Products Regulatory Agency (MHRA). However, the interpretation and
conclusions contained in this study are those of the authors alone. Access to
the General Practice Research Database was funded through the Medical Research
Council’s licence agreement with MHRA. We thank Tarita Murray-Thomas at the
MHRA for producing the dataset, and all contributing general practitioners and
their patients. PC is a senior investigator for the National Institute for
Health Research. Contributors: SW, MF, SS, and IC had the original idea for this
study. SW and MF were responsible for study hypotheses, design, data
specification, analysis, and drafting of the manuscript. MF and HP undertook
the analyses, and results were interpreted by all authors. PC advised on data
analysis and interpretation of the study findings. MF had full access to all
the data in the study and takes responsibility for the integrity of the data
and the accuracy of the data analysis. All authors contributed to the drafting
of the manuscript. SW is the guarantor. Funding: This study received no specific funding. This project
was awarded a licence as part of a scheme operated by the UK Medical Research
Council and Medicines and Healthcare products Regulatory Agency to provide data
access on up to 100 000 patients. Data were based on records from 273 primary
care practices in England, Scotland, Wales, and Northern Ireland. The providers
of this license did not have any involvement in the conduct of the research and
were not consulted in the drafting of the manuscript. Competing interests: All authors have completed the ICMJE
uniform disclosure form at www.icmje.org/coi_disclosure.pdf and declare: no support from any
organisation for the submitted work; no financial relationships with any
organisations that might have an interest in the submitted work in the previous
three years; no other relationships or activities that could appear to have
influenced the submitted work. Ethical approval: This project was approved by the Warwick
Medical School Biomedical Research Ethics Committee (reference 192-03-2012). Data sharing: No additional data available. The study
data
remain the property of the Clinical Practice Research Datalink (formerly
General Practice Research Database) and was provided to the authors under
license. Transparency: SW (the manuscript’s guarantor) affirms that the
manuscript is an honest, accurate, and transparent account of the study being
reported; that no important aspects of the study have been omitted; and that
any discrepancies from the study as planned (and, if relevant, registered) have
been explained. |
|
1. ↵ Tsimtsiou Z, Ashworth M, Jones R. Variations in
anxiolytic and hypnotic prescribing by GPs: a cross-sectional analysis using
data from the UK Quality and Outcomes Framework. Br J Gen Pract2009;59:e191-8. 2. ↵ NHS Prescription Services. Central nervous system national
charts. NHS Business Services Authority, 2012. 3. ↵ Royal College of General Practitioners and Royal College
of
Psychiatrists. Addiction to medicines consensus statement 2013. www.rcgp.org.uk/news/2013/january/addiction-to-medicines-consensus-statement.aspx. 4. ↵ Huedo-Medina TB, Kirsch I, Middlemass J,
Klonizakis M, Siriwardena AN. Effectiveness of non-benzodiazepine hypnotics in
treatment of adult insomnia: meta-analysis of data submitted to the Food and
Drug Administration. BMJ2012;345:e8343. 5. ↵ Glass J, Lanctôt KL, Herrmann N, Sproule BA,
Busto UE. Sedative hypnotics in older people with insomnia: meta-analysis of
risks and benefits. BMJ2005;331:1169. 6. ↵ Billioti de Gage S, Begaud B, Bazin F, Verdoux
H, Dartigues J-F, Peres K, et al. Benzodiazepine use and risk of dementia:
prospective population based study. BMJ2012;345:e6231. 7. ↵ Gallacher J, Elwood P, Pickering J, Bayer A,
Fish M, Ben-Shlomo Y. Benzodiazepine use and risk of dementia: evidence from
the Caerphilly Prospective Study (CaPS). J Epidemiol Community Health2012;66:869-73. 8. ↵ Wu CS, Ting TT, Wang SC, Chang IS, Lin KM.
Effect of benzodiazepine discontinuation on dementia risk. Am J Geriatr
Psychiatry2011;19:151-9. 9. ↵ Kripke DF. Chronic hypnotic use: deadly risks,
doubtful benefit. Sleep Med Rev2000;4:5-20. 10. ↵ Paterniti S, Dufouil C, Alpérovitch A. Long-term
benzodiazepine use and cognitive decline in the elderly: the Epidemiology of
Vascular Aging Study. J Clin Psychopharmacol2002;22:285-93. 11. ↵ Barker MJ, Greenwood KM, Jackson M, Crowe SF.
Cognitive effects of long-term benzodiazepine use: a meta-analysis. CNS
Drugs2004;18:37-48. 12. ↵ Kripke DF. Greater incidence of depression with
hypnotic use than with placebo. BMC Psychiatry2007;7:42. 13. ↵ Neutel CI. Risk of traffic accident injury after
a prescription for a benzodiazepine. Ann Epidemiol 1995;5:239-44. 14. ↵ Berry SD, Lee Y, Cai S, Dore DD.
Nonbenzodiazepine sleep medication use and hip fractures in nursing home
residents. JAMA Intern Med2013:1-8. 15. ↵ Kripke DF. Possibility that certain hypnotics
might cause cancer in skin. J Sleep Res2008;17:245-50. 16. ↵ Mallon L, Broman JE, Hetta J. Is usage of
hypnotics associated with mortality? Sleep Med2009;10:279-86. 17. ↵ Kao CH, Sun LM, Su KP, Chang SN, Sung FC, Muo
CH, et al. Benzodiazepine use possibly increases cancer risk: a
population-based retrospective cohort study in Taiwan. J Clin Psychiatry2012;73:e555-60. 18. ↵ Obiora E, Hubbard R, Sanders RD, Myles PR. The
impact of benzodiazepines on occurrence of pneumonia and mortality from
pneumonia: a nested case-control and survival analysis in a population-based
cohort. Thorax2013;68:163-70. 19. ↵ Hausken AM, Skurtveit S, Tverdal A. Use of
anxiolytic or hypnotic drugs and total mortality in a general middle-aged
population. Pharmacoepidemiol Drug Saf2007;16:913-8. 20. ↵ Belleville G. Mortality hazard associated with
anxiolytic and hypnotic drug use in the national population health survey. Can
J Psychiatry2010;55:558-67. 21. ↵ Hartz A, Ross JJ. Cohort study of the
association of hypnotic use with mortality in postmenopausal women. BMJ Open2012:e001413. 22. ↵ Charlson F, Degenhardt L, McLaren J, Hall W,
Lynskey M. A systematic review of research examining benzodiazepine-related
mortality. Pharmacoepidemiol Drug Saf2009;18:93-103. 23. ↵ Kripke DF, Langer RD, Kline LE. Hypnotics’
association with mortality or cancer: a matched cohort study. BMJ Open2012:2:e000850. 24. ↵ Gisev N, Hartikainen S, Chen TF, Korhonen M,
Bell JS. Mortality associated with benzodiazepines and benzodiazepine-related
drugs among community-dwelling older people in Finland: a population-based
retrospective cohort study. Can J Psychiatry2011;56:377-81. 25. ↵ Vinkers DJ, Gussekloo J, Van der Mast RC, Zitman
FG, Westendorp RGJ. Benzodiazepine use and risk of mortality in individuals
aged 85 years or older. JAMA2003;290:2942-3. 26. ↵ Kripke DF, Klauber MR, Wingard DL, Fell RL,
Assmus JD, Garfinkel L. Mortality hazard associated with prescription hypnotics. Biol Psychiatry1998;43:687-93. 27. ↵ Tiihonen J, Suokas JT, Suvisaari JM, Haukka J,
Korhonen P. Polypharmacy with antipsychotics, antidepressants, or
benzodiazepines and mortality in schizophrenia. Arch Gen Psychiatry2012;69:476-83. 28. ↵ Khan NF, Harrison SE, Rose PW. Validity of
diagnostic coding within the General Practice Research Database: a systematic
review. Br J Gen Pract2010;60:e128-36. 29. ↵ BMA and Royal Pharmaceutical Society of Great
Britain. British national formulary. 63 ed. BMJ Group and RPS Publishing, 2012. 30. ↵ Solomon MD, Majumdar SR. Primary non-adherence
of medications: lifting the veil on prescription-filling behaviors. J
Gen Internl Med2010;25:280-1. 31. ↵ Fischer MA, Stedman MR, Lii J, Vogeli C, Shrank
WH, Brookhart MA, et al. Primary medication non-adherence: analysis of 195,930
electronic prescriptions. J Gen Intern Med2010;25:284-90. 32. ↵ WHO Collaborating Centre for Drug Statistics Methodology.
Guidelines for ATC classification and DDD assignment 2012. WHO Collaborating
Centre for Drug Statistics Methodology, 2011. 33. ↵ Savitz DA, Baron AE. Estimating and correcting
for confounder misclassification. Am J Epidemiol1989;129:1062-71. 34. ↵ Fewell Z, Davey Smith G, Sterne JAC. The impact
of residual and unmeasured confounding in epidemiologic studies: a simulation
study. Am J Epidemiol2007;166:646-55. 35. ↵ Lawlor DA, Smith GD, Bruckdorfer KR, Kundu D,
Ebrahim S. Those confounded vitamins: what can we learn from the differences
between observational versus randomised trial evidence? Lancet2004;363:1724-7. 36. ↵ Lévesque LE, Hanley JA, Kezouh A, Suissa S.
Problem of immortal time bias in cohort studies: example using statins for
preventing progression of diabetes. BMJ2010;340:b5087. 37. ↵ Cole SR, Platt RW, Schisterman EF, Chu H,
Westreich D, Richardson D, et al. Illustrating bias due to conditioning on a
collider. Int J Epidemiol2010;39:417-20.
INTERNAL SITE SEARCH ENGINE by Google
|