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Original Article

Evaluating Short-Term Drug Effects Using a Physician-Specific Prescribing Preference as an Instrumental Variable

Brookhart, M Alan; Wang, Philip S.; Solomon, Daniel H.; Schneeweiss, Sebastian

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doi: 10.1097/01.ede.0000193606.58671.c5
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Postmarketing observational studies are often conducted to evaluate the safety and effectiveness of drugs as they are used in routine practice. These studies are necessary because clinical trials often exclude populations that ultimately use the drug such as the elderly, children, pregnant women, and patients with chronic illnesses.1 Furthermore, because clinical trials are underpowered to detect uncommon adverse events, nonexperimental postmarketing studies are needed to evaluate the safety of approved drugs.2,3 This function of postmarketing research has come under increased scrutiny with the recent safety concerns pertaining to several widely used therapeutic agents, including selective COX-2 inhibitors, hormone replacement therapy, and selective serotonin reuptake inhibitors.

Studies of outcomes associated with exposure to pharmaceutical products as they are used in routine practice are inherently nonexperimental. Often such studies are based on healthcare claims data containing longitudinal information on pharmacy dispensing, healthcare encounters, procedures, and International Classification of Diseases-coded diagnoses.4 Although these files contain data on large populations followed over extended periods of time, they often lack detailed information on clinical indications for specific therapies. This problem is thought to be particularly acute in studies of intended drug effects because of the difficulty in adjusting for confounding by indication5; ie, patients who are thought to benefit most from a drug are more likely to receive therapy.6–8 Although epidemiologists have a variety of design options and analytic tools to adjust for measured confounders, pharmacoepidemiologic studies have consistently been criticized for having incomplete information on many potential predictors of study outcomes that might lead to selective prescribing.9–13 Some authors argue that it is impossible for current epidemiologic methods to fully adjust confounding by indication in studies of intended drug effects.14

Ecologic, grouped treatment and instrumental variable methods have been proposed as potential approaches to address confounding by indication in clinical epidemiology.15–21 These methods attempt to reduce bias through the use of a variable (an “instrument”) that is related to treatment but unrelated to the unobserved patient risk factors that confound conventional statistical approaches. Unfortunately, it is difficult to find high-quality instruments in drug epidemiology. Hospital- or region-level instruments have been used when substantial variations in practice patterns are thought to exist. The use of individual physicians as instruments has been proposed for situations in which physicians are thought to vary in their preference for different treatments under study.22

In this article, we explore the use of a physician-level instrumental variable for studies that compare the short-term effects of 2 or more competing drug therapies. The instrument that we consider is a time-varying estimate of a physician's relative preference for each of the therapeutic alternatives under study. We develop this idea in a study of the short-term effects of COX-2 inhibitor use on gastrointestinal (GI) toxicity compared with nonselective nonsteroidal antiinflammatory drugs (nonselective NSAIDs). This example was chosen for 3 reasons: (1) conventional claims-data studies of the intended effects of COX-2 inhibitor use are known to be problematic because of residual confounding by unmeasured factors, including aspirin use, body mass index, physical activity, smoking status, alcohol consumption, and subtle GI symptoms not recorded in claims data; (2) recent research showed that physicians appear to differ substantially in their preference for prescribing COX-2 inhibitors compared with nonselective NSAIDs23–26; and (3) randomized, controlled trial (RCT) results are available, indicating a causal relation between COX-2 use and reduced GI toxicity and providing an accepted reference standard.



Our study population comprised a cohort of new oral NSAID users among Medicare beneficiaries age 65 years and older concurrently enrolled in the Pharmaceutical Assistance Contract for the Elderly (PACE) provided by the state of Pennsylvania. PACE has more generous income eligibility criteria than Medicaid and includes patients above the poverty level. (To be eligible for PACE, the annual income must be less than $13,000 if single and less than $16,200 if married.) The program reimburses the cost of all prescription medications, including selective COX-2 inhibitors and nonselective NSAIDs, with a $6 copayment. Enrollees of PACE were eligible for inclusion in the study if they filled a prescription for an oral preparation of a nonselective NSAID or selective COX-2 inhibitor (celecoxib, rofecoxib, valdecoxib) between 1 January 1999 and 31 July 2002 and demonstrated continuous healthcare system use. We defined continuous use as filling at least one prescription drug and using healthcare services during each of the 3 6-month periods before the index date defined subsequently.

First-time NSAID use was defined as being an eligible beneficiary who filled at least one prescription for any oral preparation for an NSAID (either a COX-2 inhibitor or a nonselective NSAID) between 1 January 1999 and 31 July 2002 but did not use any NSAID during 18 months before the index date. The index date was the first date an NSAID prescription was filled. The analysis was limited to first-time users because a physician's evaluation of patient risk factors would likely precede the first COX-2 inhibitor or nonselective NSAID prescription. We did not consider any prescriptions after the index prescription.

Prescription drug information was assessed based on pharmacy claims from PACE. Computerized records include prescription drug name, dosage, quantity dispensed, days supplied, date dispensed, and the Universal Physician Identification Number for the prescribing physician. Outpatient and inpatient diagnoses, procedure codes, and dates of all inpatient and outpatient services obtained from Medicare claims data were linked to pharmacy-dispensing data. Miscoding of drug information and misclassification of relevant International Classification of Diseases, 9th Revision (ICD-9) diagnoses are described as small or moderate.27–30 No information was available on over-the-counter NSAID or aspirin use, but beneficiary surveys have shown that over-the-counter aspirin use is similar in COX-2 and nonselective NSAID users in this population.31 We omitted patients for whom the initial NSAID prescription did not contain a valid physician code. We obtained physician specialty information by linking the physician number to the American Medical Association's (AMA) Masterfile of Physicians. The AMA Masterfile has been found to be a reliable source of information about physician specialty.32

All personal identifiers were removed from the analytic data files to protect the privacy of subjects and their physicians. The study was approved by the Institutional Review Board of Brigham and Women's Hospital, Boston. We obtained Data Use Agreements from PACE and the Center for Medicare and Medicaid Services.

Study Outcomes

GI complications were defined as either a hospitalization for GI hemorrhage or peptic ulcer disease, including perforation (primary ICD-9 discharge diagnosis code 531.x, 532.x, 533.x, 534.x, 535.x in the first or second position) or an outpatient visit for a GI hemorrhage. These definitions were validated in 1762 patients in a hospital discharge database in Saskatchewan with a composite positive predictive value (PPV) of 90%33; similar PPVs were found in a regional Spanish discharge database.34

Statistical Analysis

We estimated the effect of short-term COX-2 inhibitor use on GI complications compared with nonselective NSAIDs using conventional multivariable regression methods and an instrumental variable approach.

Instrumental variable analysis is a statistical approach that can be used to estimate a treatment effect in the presence of unmeasured confounding factors.35,36 The approach depends on the existence of a variable (termed an instrument or instrumental variable) that is causally related to treatment but unrelated to a patient's potential (counterfactual) outcomes.37,38 Therefore, an instrumental variable is an external factor that influences an outcome only through its effect on treatment.

The central issue in an instrumental variable analysis is the quality of the instrument. Any direct relation between the supposed instrument and the confounders or outcome can lead to bias in the estimated exposure effect. One cannot confirm the absence of these relations with data, but investigators often report the association between the instrument and the measured patient characteristics. An instrumental variable analysis can adjust for measured patient characteristics; however, if the instrument is related to observed patient characteristics, then it is reasonable to expect that it may be related to important unobserved variables. A high-quality instrument also should be strongly related to treatment. The variance and bias of an instrumental variable estimator depend on the strength of this relation. More detailed discussions of instrumental variable methods and their assumptions can be found elsewhere.35,37

Our conceptual instrument is a physician's current preference for a COX-2 inhibitor relative to a nonselective NSAID. The assumed causal relations motivating this choice of instrument are shown in Figure 1. The assumption that physicians vary in their NSAID preference implies that certain patients would be treated with a nonselective NSAID by some physicians and with a COX-2 inhibitor by others. For a physician's preference to be a valid instrument, there can be no direct arrow from preference to the outcome. This requires that physicians can influence short-term NSAID-related GI toxicity only through the type of NSAID prescription that they assign. It is also necessary that there be no arrow between physician preference and the patient-level confounders. This assumption will be satisfied if physicians who prefer COX-2 inhibitors are not treating patients who systematically differ from the patients of physicians who prefer nonselective NSAIDs.

Diagram of the causal relations motivating the instrumental variable analysis.

Unfortunately, a physician's drug preference is a variable that is not easily measured. Furthermore, preference can change quickly in response to marketing activities by pharmaceutical companies, new information about the safety and efficacy of a drug, and the physician's own evolving clinical experience. The dynamic aspect of preference is particularly relevant with COX-2 inhibitors that were aggressively marketed, adopted rapidly by some physicians, more slowly by others, and then subject to a variety of safety concerns that could have discouraged their use.24

We propose to estimate a physician's current preference for a COX-2 inhibitor relative to a nonselective NSAID by using the type of the most recent, new NSAID prescription written by that physician. According to this approach, if the last new NSAID prescription was for a COX-2 inhibitor, then for the next patient, the physician is classified as a “COX-2 prescriber.” Otherwise, the physician is classified as a “nonselective NSAID prescriber.” We also consider an alternative estimate of preference based on the historical proportion of a physician's new NSAID prescriptions that were for a COX-2 inhibitor. This is arguably a more biased but less variable estimate of preference.

To describe the statistical models used to estimate the effect of COX-2 inhibitors on GI toxicity, we introduce the following notation: let Z be the instrument indicating the last new NSAID prescription written by the patient's physician (if the last new NSAID prescription written was for a COX-2 inhibitor, then Z = 1; otherwise, Z = 0); let Y be the disease outcome (GI complication within 60, 120, or 180 days); let X be a variable indicating whether a patient was actually exposed to a COX-2 inhibitor (X = 1 if the patient was treated with a COX-2 inhibitor, otherwise X = 0); and let all confounders be contained in the p-dimensional vector C. The parameter of interest is the risk difference (RD), ie, the risk of a GI complication due to COX-2 use minus the risk of a GI complication due to nonselective NSAID use. We report a rescaled RD that is derived by multiplying the risk difference by 100 (ie, the change in risk per 100 patients treated). We estimate this parameter in 4 ways: a crude RD, a multivariable-adjusted RD, an unadjusted instrumental variable estimate of the RD, and an adjusted instrumental variable estimate of the RD.

The statistical approaches we use are based on standard linear regression models. To estimate the crude risk difference, we fit a simple linear regression model of the disease outcome on the exposure:

The adjusted risk difference is derived from least-squares estimation of a multivariable linear regression model that contains the exposure and the confounders:

Our instrumental variable estimators are derived by 2-stage least-squares. For the unadjusted estimator, the first stage involves estimating the expected value of the exposure given the instrument,

. This is done by taking the relative frequency of COX-2 exposure for Z = 1 and Z = 0. In the second stage, we fit the simple linear regression model:

For this model, least-squares estimation of δ leads to the following estimator of the RD:


is the relative frequency of the outcome within strata of the instrument. For the adjusted instrumental variable estimator, in the first stage, we estimate the expected value of the exposure given the instrument and confounders through least-squares estimation of the linear model:

In the second stage, we use the predicted values from the first stage and least squares to fit the linear model:

These models were fit to the full study population using 3 different definitions of the follow-up period: 60, 120, and 180 days from the index date. We conducted a restricted analysis looking at only patients of primary care physicians. By eliminating patients whose prescriptions were started by a specialist physician, we hoped to create a more homogeneous patient mix with respect to unmeasured variables. We also conducted an analysis restricted to patients with a diagnosis of osteoarthritis or rheumatoid arthritis because these were the patient populations included in the 2 major RCTs that examined the gastrointestinal effects of COX-2 inhibitors.39,40

All analyses were done using the GENMOD procedure in SAS version 9.1 and the instrumental variable estimation procedure (ivreg) in Stata 7.0. Standard errors were estimated robustly to account for the clustering of patient-level observations within physicians.


We identified 50,548 new starters of either a COX-2 inhibitor or nonselective NSAID between 1 January 1999 and 31 July 2002. Of these, 629 were excluded because of missing or invalid physician information associated with the pharmacy claim. Of the remaining 49,919, 17,646 (35%) were started on a nonselective NSAID, whereas 32,273 (65%) were placed on a COX-2 inhibitor. The characteristics of the sample are given in Table 1.

Characteristics of Patients Stratified on Type of NSAID Prescription Assigned at Index Date

There were strong associations between all measured patient-level characteristics and the actual use of COX-2 inhibitors (Table 2, column 1). Patients placed on COX-2 inhibitors were older, had more comorbidities, and were much more likely to have risk factors for NSAID associated GI toxicity such as the use of warfarin, glucocorticoids, and a history of peptic ulcer disease and upper GI bleeds. Although some of these characteristics were still associated with the instrumental variable in the full population (Table 2, column 2), the associations were strongly attenuated. The presence of some residual associations suggests that the instrumental variable assumptions are not completely satisfied. When we further restrict this analysis to patients of primary care physicians, the associations between the instrument and the risk factors were not substantially changed from the associations seen in the full population (Table 2, column 3).

Associations Between Patient Risk Factors and Actual Treatment, the Instrumental Variable, and the Instrumental Variable in a Sample Restricted to Patients of Primary Care Physicians

As required, the instrument was also related to treatment. Across the entire population, if the last prescription written by a physician was for a COX-2 inhibitor, then the probability that the next prescription would be for a COX-2 inhibitor was 77%. On the other hand, if the last prescription written by a physician was for a nonselective NSAID, then the probability that the next prescription would be for a COX-2 was only 55%. Among patients of primary care physicians, these probabilities were nearly identical (77% and 57%).

In Table 3, we present unadjusted associations between the actual treatment and the outcome, and also between the instrument and the outcome. For all follow-up periods and restriction criteria, there was a positive association between COX-2 inhibitor exposure and the occurrence of a GI complication. The instrumental variable, however, was consistently associated with a reduced risk of a GI complication.

Unadjusted Associations Between Treatment Received and Outcome and Between Instrumental Variable and Outcome

The estimated risk differences according to the various statistical approaches are presented in Table 4. None of the conventional analyses suggested a risk reduction in GI toxicity with COX-2 inhibitor use relative to nonselective NSAIDs. For all estimates derived from conventional statistical models, the estimates of risk difference were close to zero with narrow confidence intervals that included zero. However, results from both the adjusted and unadjusted instrumental variable analysis suggest a protective effect of COX-2 exposure compared with nonselective NSAIDs. For the full population, the point estimate ranged from a risk reduction of 0.9 to 1.3 events per 100 patients. When the analysis was restricted to primary care physicians and when the time interval was extended to 180 days, the point estimates were slightly attenuated. For the analysis restricted to patients with osteoarthritis and rheumatoid arthritis, the estimated protective effect of COX-2 exposure was more pronounced with point estimates of the risk reduction ranging from 1.5 to 2.1 events per 100 patients.

Instrumental Variable and Conventional Multivariable Regression Estimates of the Risk Differences of Gastrointestinal Toxicity per 100 Patients Treated With COX-2 Inhibitors Compared With Nonselective NSAIDs

The conventional multivariable analysis was able to use more patients than the instrumental variable approach because the instrument is undefined for the first patient prescribed an NSAID by each physician during the study period. To explore whether sample differences could be influencing our results, we restricted the conventional analysis to the same set of patients used by the instrumental variable method. This approach yielded similar parameter estimates as the conventional method applied to the full sample. Our alternative instrumental variable analysis, which estimated preference using the historical proportion of a physician's new NSAID prescriptions that were for a COX-2 inhibitor, yielded estimates that were attenuated but still suggestive of a protective effect.


Contrary to RCT results showing that COX-2 inhibitors reduce the risk of GI complications relative to nonselective NSAIDs,39,40 our conventional multivariable analysis found no evidence of a gastroprotective effect of COX-2 inhibitors. Although we do not know the true degree of protection afforded by COX-2 inhibitors in our population, the absence of any apparent protective effect is more plausibly attributable to residual confounding by unmeasured patient characteristics rather than to a total absence of an effect.

In contrast to the conventional analysis, our instrumental variable approach yielded evidence of a clinically significant protective effect due to COX-2 exposure, particularly for shorter-term drug exposures. In Table 5, we compare the results obtained from the adjusted instrumental variable approach with results from the VIGOR and CLASS trials.39,40 Because these trials studied populations with rheumatoid arthritis and/or osteoarthritis, the instrumental variable estimates restricted to those patients are the most relevant. For all follow-up periods considered, the instrumental variable estimates are statistically similar to the trial results. However, for 60- and 120- day periods, the instrumental variable estimates are substantially larger in absolute magnitude. This suggests that in our population, which is older and more frail than the trial population, COX-2 inhibitors may have a greater protective effect. The attenuation of the instrumental variable estimate at 180 days is compatible with the nonadherence and treatment crossover that is to be expected in an uncontrolled routine care setting.

Comparison of Adjusted Instrumental Variable Estimates to Randomized Trial Results

Instrumental variable methods are not commonly used in epidemiology, so readers may find the approach proposed in this article to be counterintuitive. One might question how the treatment assignment of one patient can be coupled with the outcome of another patient to estimate an exposure effect. For the case of NSAIDs, we have argued that treatment assignment depends on both physician preference and patient risk factors. The observation that NSAID-prescribing depends partly on physician preference suggested the possibility that individual physicians could be used as the basis of a natural experiment. Because physician preference was unmeasured and dynamic, we used the last new NSAID prescription written as an estimate of the physician's current preference. This led to a conceptual natural experiment in which the last prescription written becomes the “treatment arm assignment” for the next patient. An intention-to-treat analysis of this natural experiment would be reasonable; however, intention-to-treat estimates tend to be biased toward the null. Instrumental variable estimators are an alternative to intention-to-treat methods and under certain assumptions can provide asymptotically unbiased estimates of treatment effects for both natural and randomized experiments in which treatment received is confounded. The unadjusted instrumental variable estimate is an inflated intention-to-treat estimate of the risk difference in which the inflation factor depends on the marginal probability of treatment in each arm.

Although the estimates from the instrumental variable approach proposed in this article are consistent with RCT results, the method and results should be interpreted with caution. In our example, physicians who are frequent users of COX-2 inhibitors are seeing higher-risk patients as evidenced by the association between some of the observed risk factors and the instrument. Although the instrumental variable estimate can be adjusted for these observed risk factors, it is reasonable to expect that the instrument may be related to the unobserved risk factors that confound the conventional analysis. In such a situation, some of what appears to be physician preference for a COX-2 inhibitor will actually be a clustering of high-risk patients within a particular practice. This clustering phenomenon leads to a violation of the instrumental variable assumptions and subsequent bias in the estimator. However, if there are important unmeasured confounders, then standard statistical estimates of the exposure effect will also be biased.

By using a variable that is strongly related to treatment, but only weakly related to unobserved risk factors, we hope to derive an estimate for which the confounding is strongly attenuated. We noted that the adjusted instrumental variable estimate was very close to the unadjusted estimate, indicating that the residual confounding in the unadjusted estimate due to the association between the instrument and the measured risk factors was small. This leads us to speculate that the residual confounding due to the association between the instrument and the unmeasured risk factors may be similarly small. However, this conclusion cannot be verified from the data. Instruments that are weakly related to both treatment and the unobserved confounders can result in estimates that are more biased than conventional regression estimates. Analytic work, simulation studies, and sensitivity analyses need to be done to understand how the bias in this instrumental variable approach compares with the bias of regression estimates under realistic assumptions about unobserved confounding and the clustering of those confounders within individual physicians.

Another potential source of bias in the instrumental variable method results from the possibility that a physician can influence the outcome in ways other than through the prescribing of an NSAID. For example, physicians who frequently prescribe COX-2 inhibitors may also be more likely to coprescribe proton pump inhibitors for additional GI protection. In such a situation, the protective effect of COX-2 exposure is partly attributable to the joint use of a proton pump inhibitor. In principle, it would be possible to remove this bias by creating additional treatment categories related to these combination therapies. Instrumental variable methods could then be used to simultaneously estimate the effect of each competing therapy.

One final limitation in our study is the lack of an untreated comparison group. This results from our inability to identify the moment when a physician decides not to assign treatment to a patient who might be a candidate for new NSAID therapy. The lack of a untreated group imposes an additional assumption on the instrumental variable, namely that it is unrelated to the decision to not assign treatment. In the case of NSAIDs, this assumption is reasonable. However, an ideal design would select patients for inclusion in the study based on an incident diagnosis associated with a visit to a physician rather than the initiation of a new prescription.

For different drug-exposure studies, alternative methods of estimating preference could be considered. If physician preference is not thought to change over time, preference can be estimated from the proportion of prescriptions written for a particular drug across the entire study period. When preference changes over time and there are sufficient numbers of patients per physician, more complex time-varying estimates of preference are possible. For example, the relative frequency of recently written COX-2 prescriptions could be used as an estimate of current preference. Given a set of alternative estimates of physician preference, the analyst should select the estimate that appears to be the most strongly related to the observed treatment among those estimates that are unrelated to observed patient characteristics.

Despite the limitations of the proposed instrumental variable analysis, it is intriguing that this approach is able to attribute a protective effect to COX-2 exposure similar to what was observed in RCTs. When all the important confounders are measured, conventional statistical methods are the most appropriate way to analyze observational data in pharmacoepidemiology. For analyses of intended drug effects, however, it is often the case that many important confounders are unmeasured. Instrumental variable methods have been understudied in drug epidemiology and merit further consideration as a potential approach to deal with the vexing problem of confounding by unmeasured indication.


We acknowledge the helpful comments of Kenneth Rothman, Barry Kitch, Colin Dormuth, and Til Stürmer.


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