Drug-Drug Interaction Surveillance Study: Comparing Self-Controlled Designs in Five Empirical Examples in Real-World Data

Abstract

Self-controlled designs, specifically the case-crossover (CCO) and the self-controlled case series (SCCS), are increasingly utilized to generate real-world evidence (RWE) on drug-drug interactions (DDIs). Although these designs share the advantages and limitations of within-individual comparison, they also have design-specific assumptions. It is not known to what extent the differences in assumptions lead to different results in RWE DDI analyses. Using a nationwide US commercial healthcare insurance database (2006–2016), we compared the CCO and SCCS designs, as they are implemented in DDI studies, within five DDI-outcome examples: (1) simvastatin + clarithromycin and muscle-related toxicity; (2) atorvastatin + valsartan, and muscle-related toxicity; and (3–5) dabigatran + P-glycoprotein inhibitor (clarithromycin, amiodarone, and verapamil) and bleeding. Analyses were conducted within person-time exposed to the object drug (statins and dabigatran) and adjusted for bias associated with the inhibiting drugs via control groups of individuals unexposed to the object drug. The designs yielded similar estimates in most examples, with SCCS displaying better statistical efficiency. With both designs, results varied across sensitivity analyses, particularly in CCO analyses with small number of exposed individuals. Analyses in controls revealed substantial bias that may be differential across DDI-exposed and control individuals. Thus, both designs showed no association between amiodarone or verapamil and bleeding in dabigatran-exposed but revealed strong positive associations in controls. Overall, bias adjustment via a control group had a larger impact on results than the choice of a design, highlighting the importance and challenges of appropriate control group selection for adequate bias control in self-controlled analyses of DDIs.

Electronic healthcare databases are increasingly utilized to identify drug-drug interactions (DDIs) and generate real-world evidence (RWE) on their clinical impact.^1-3 Rigorous use of real-world data (RWD), however, presents many challenges because treatments are not randomized in clinical practice, relevant information on exposures, confounders, or outcomes may be missing, and inappropriate study design or violations of assumptions required for valid causal inference may lead to biased estimates.^4,5

Although a cohort design, which is an observational analogue of a parallel group randomized clinical trial, is the most common design applied in observational research of drug outcomes, in general, and of DDIs in particular,⁶ self-controlled designs, in which individuals are compared with themselves, have also shown promise for RWD DDI research, particularly when no appropriate comparison treatment is available or when several drugs are assessed simultaneously (e.g., in a high-throughput identification of potential DDIs in large databases).^1,7,8 As compared with other observational study designs, self-controlled designs have the unique attribute of inherently controlling for all potential confounders that are stable over the study period, including those that are unmeasured and unknown.^9-11

Self-controlled designs comprise a variety of methods; however, the two main study designs that have been implemented for RWD DDI studies are the case-crossover (CCO) and the self-controlled case series (SCCS).^7,12,13 Both designs analyze only individuals who experience the outcome (cases) and use each individual as his or her own control. Both inherently control for risk factors that remain stable within individuals but will produce biased estimates in the presence of time-varying, within-person confounding.¹⁴ The key difference between the two designs is that the CCO is indexed on the outcome and usually compares the odds of exposure prior to the outcome (hazard window) to the odds of exposure at some preselected control time (referent window; Figure 1), whereas the SCCS design is indexed on the exposure and compares the rate of outcome incidence during exposed person-time to the rate during unexposed (control) person-time (Figure 1). Unlike the CCO design, which samples person-time, the SCCS design utilizes all person-time available. Moreover, as traditionally implemented in studies of medications, the CCO design samples person-time prior to the outcome (unidirectional), essentially censoring patients on outcome occurrence, whereas in SCCS analyses follow-up continues after an outcome. These differences lead to design-specific assumptions for valid estimation: constant exposure probability across the referent and hazard windows in a CCO, and no outcome-dependent exposure change or censoring in SCCS.^9,11 Although these assumptions and their violation in the context of DDI analyses have been investigated in a simulation study,¹⁴ it is not known to what extent the differences in assumptions lead to different results produced by the CCO and the SCCS designs in RWD analyses. Therefore, we aimed to compare these two designs using five DDI empirical examples and a large, US-based, commercial healthcare insurance database.

Figure 1.

Case-crossover (CCO) and self-controlled case series designs for real-word data drug-drug interaction studies. In a CCO study, odds of exposure (to the precipitant drug) during the hazard window are compared to the odds of exposure during the referent window. In the self-controlled case series study, outcome incidence rates during the exposed (to the precipitant drug) person-time are compared with the rates during the unexposed person-time.

METHODS

The research was approved by Partners Healthcare Institutional Review Board. As data are de-identified, the need for informed consent was waived. A data use agreement was in place. Protocol is presented in the Supplementary Materials.

Data source

Data for this investigation came from IBM Truven Health MarketScan research databases (the MarketScan Commercial Claims and Encounters database and Medicare Supplemental database; January 1, 2006 – December 31, 2016). These databases comprise longitudinal claims data that include both inpatient and outpatient diagnoses and procedures, as well as claims for both standard and mail order prescription drug dispensing with information on product dispensed (captured via National Drug Code (NDC)), quantity dispensed, and days’ supply. Overall, these databases provide longitudinal information on > 100 million individuals, and are commonly utilized for RWE analyses, including those of DDIs.

Empirical examples

We evaluated five empirical examples: (1) simvastatin, a substrate of cytochrome P450 (CYP) 3A4 enzyme, and clarithromycin, a CYP3A4 inhibitor; (2) atorvastatin, a substrate of the OATP 1B1 membrane influx transporter, and valsartan, a potential OATP1B1 inhibitor; and (3-5) dabigatran etexilate, a P-gp substrate, and P-gp inhibitors (clarithromycin, amiodarone, and verapamil). The examples were chosen because they represented DDIs with pharmacological evidence of a potential interaction,^15-20 and could be validly assessed in healthcare insurance claims (Table 1).⁴ We also aimed to include examples with short-term and chronic precipitants, as some prior work suggested that self-controlled designs may be less susceptible to bias when exposures are brief.^10,14 Finally, our examples represented a range of scenarios with varying degrees of pharmacokinetic inhibition and clinical DDI awareness. Simvastatin-clarithromycin represented a well-established interaction. The concomitant use of these drugs has been contraindicated in the United States since June 2011²¹ and least one prior cohort study confirmed the increased risk of rhabdomyolysis among patients exposed to both agents.²² The clinical impact of other DDIs is less clear. Pharmacokinetic studies showed small increases in dabigatran concentration following administration of clarithromycin, but bigger increases following administration of amiodarone or verapamil²³; as of November 2020, all 3 interactions were listed as major in IBM Micromedex and as moderate in Lexicomp. Valsartan has been shown to be a potential inhibitor of OATP1B1, although the clinical implication of this inhibition is unclear^15,24; no interaction between atorvastatin, an OATP1B1 substrate, and valsartan is listed in either Micromedex or Lexicomp databases.

Table 1.

Summary of empirical examples

	Object drug	Precipitant drug	Clinical outcome	Mechanism of interaction
1	Simvastatin	Clarithromycin	Muscle-related toxicity	CYP3A4 inhibition
2	Atorvastatin	Valsartan	Muscle-related toxicity	OATP1B1 inhibition
3	Dabigatran	Amiodarone	Major bleeding	P-gp inhibition
4	Dabigatran	Verapamil	Major bleeding	P-gp inhibition
5	Dabigatran	Clarithromycin	Major bleeding	P-gp inhibition

Study population and study designs

Study population included individuals at least 18 years of age who experienced the outcome of interest during 2006–2016 (2010–2016 for dabigatran examples) and were exposed to the precipitant drug of interest during the observation period. To evaluate DDIs, only person-time on the object drug of interest was evaluated, and patients were required to be on the object drug continuously during the observation period (Figure 1). Such an approach controls for confounding by indication for the object drug and is often implemented in self-controlled studies of DDIs.^1,6,25

In CCO analyses, odds of exposure to the precipitant drug during the hazard window were compared with the odds of exposure to the precipitant drug during the referent window. If individuals had more than one outcome event, we took the first one. Starting from the outcome date and moving retrospectively in time (Figure 1, top), for each analysis, we defined a 1-day induction window, a hazard window, a washout window, and a referent window of the same duration as the hazard window. Individuals were required to have continuous exposure to the object drug starting at the beginning of the referent window through the outcome date, with no exposure to other drugs from the same therapeutic class (statins or oral anticoagulants). Exposure to the precipitant was based on at least one pharmacy dispensing within a window. Individuals were required to have insurance eligibility for at least 90 days prior to the start of the referent window.

In SCCS analyses, the rates of outcome incidence during the person-time exposed to the precipitant drug were compared with the rates of outcome incidence during the person-time unexposed to the precipitant drug. Starting from the first available prescription of the object drug following at least 90 days of object-drug free enrollment (Figure 1, bottom) and continuing until object drug discontinuation, initiation of another drug from the same therapeutic class, death, or disenrollment (whichever came first), we identified periods of continuous exposure to the object drug (observation periods). Only observation periods with at least 1 day of exposure to the precipitant and at least 1 event were evaluated. Within each period, we allocated person-time exposed to the object drug into three categories: (i) unexposed, defined as not exposed to a precipitant; (ii) exposed, defined as exposed to a precipitant; and (iii) postexposure or washout, defined as the period immediately after precipitant discontinuation. The postexposure period was introduced to allow the risk to return to baseline (unexposed). Exposure to the precipitant was defined based on days’ supply and lagged by 1 day (i.e., individuals were considered exposed starting the day after the dispensing day through the day after the end of days’ supply). Time spent in the hospital at the time of the event was excluded from the analysis. All outcomes were counted. To avoid counting clusters of events as separate, we required at least 90 days between subsequent outcomes; thus, outcomes occurring within 90 days of each other were considered as one outcome with the admission date for the first occurrence set as the event date.

Because initiation or discontinuation of precipitant drugs may be associated with changes in health status that are associated with the outcome, time-varying, within-person confounding is highly likely in self-controlled analyses of DDIs. To control for bias associated with the precipitant drug, we utilized negative controls who were exposed to the precipitant drug of interest in the absence of exposure to the object drug. Adjustment via controls has been shown to validly control for time-varying confounding in self-controlled analyses under the assumption that analyses in controls approximate the bias observed in cases.^25,26 In our analyses, we required that controls were not exposed to the object drug or similar drugs from the same therapeutic class (i.e., any statins in examples with statins and any oral anticoagulants in dabigatran examples), at the time of the outcome and for the duration of the observation period.

Exposures and outcomes

Exposures and outcomes for all empirical examples are presented in Table 1. Exposures were identified based on pharmacy-recoded dispensed fills of medications of interest. Continuous exposure to the object drug was determined based on pharmacy-recorded days’ supply, allowing for a gap of 14 days (statins) or 7 days (dabigatran) between the end of the days’ supply and a subsequent refill, to allow for some delay in refilling. In the CCO analysis, exposure to the precipitant was defined based on a dispensing within a predefined window (days 2–15 preceding the outcome as hazard and days 46–59 as referent in the analyses of clarithromycin; days 2–31 as hazard and 62–91 as referent in the analyses of other precipitants). In SCCS analysis, precipitant drug exposure was defined based on a dispensing and days’ supply, lagged by 1 day (i.e., individuals were considered exposed starting the day after dispensing and through the day after the end of days’ supply).

Outcomes included hospitalizations with muscle-related toxicity (e.g., rhabdomyolysis, myoglobinuria, generalized muscle weakness, myositis, and myopathy) for both simvastatin and atorvastatin examples and major bleeding (intracranial, upper/lower gastrointestinal, and within other normally sterile sites) for dabigatran examples. Outcomes were ascertained based on hospital discharge diagnoses (Table S1), with the admission date set as the outcome date.

Statistical analysis

For both designs, we assessed mean age and sex distributions across DDI-exposed and eligible control individuals. Age was assessed on the first day of the observation period. To explore outcome-related censoring in SCCS analyses, we evaluated the distribution of time between event and censoring, and reasons for censoring across DDI-exposed and control individuals in SCCS analyses. We also plotted precipitant drug dispensing times relative to the outcome dates to explore outcome-related changes in exposure.

For CCO analyses, odds of exposure to the precipitant drug during the hazard window were compared with odds of exposure during the referent window, using conditional logistic regression stratified on individual. For SCCS analyses, event rates during the time exposed to the precipitant were compared with rates during unexposed time, using conditional Poisson models stratified on observation period.

To obtain the adjusted estimate, we fit models with an exposure term and a product term between case status (DDI-exposed or control) and exposure. The coefficient for the product term corresponds to the ratio of relative estimates obtained from (1) cases exposed to the potential DDI and (2) cases exposed to a precipitant in the absence of the object drugs (controls), yielding the association above and beyond that observed in controls.²⁷

Sensitivity and subgroup analyses

We conducted several sensitivity analyses aimed at assessing the impact of exposure misclassification. In CCO analyses, we extended the duration of either hazard and referent windows (to 17 and 21 days in the analyses of clarithromycin; to 60 and 90 days in the analyses of other precipitants; Tables S2-S4), or the washout window (from 30 to 60 days). In SCCS, we extended the duration of the postexposure window to 30 days.

For the atorvastatin-valsartan example, we conducted a sensitivity analysis limiting the outcome to rhabdomyolysis (International Classification of Diseases, Ninth Edition, Clinical Modification (ICD-9) diagnosis code of 728.88 and ICD-10 diagnosis code of M62.82), and a subgroup analysis stratifying patients based on the dose of atorvastatin (> or ≤ 20 mg daily). In the subgroup analyses, cases were required to stay within the given dose range and were censored as soon as they switched to the other dose subgroup. In addition, for the simvastatin-clarithromycin example, we conducted an SCCS sensitivity analysis evaluating first outcomes only (if individuals experienced more than one event).

In post hoc SCCS sensitivity analyses aimed to approximate observation time in DDI-exposed individuals and to decrease bias due to time-varying confounding, we limited observation time in controls to 180 days before and 180 days after the start of the precipitant drug exposure. In these analyses, individuals could still be censored due to other reasons mentioned above; however, total observation time could not exceed 360 days. Unlike outcome-dependent censoring, exposure-based censoring does not lead to bias in SCCS analyses.²⁸

All analyses were conducted using SAS 9.4 (SAS Institute, Cary, NC).

RESULTS

As eligibility requirements differed slightly between the two designs, primarily due to the variation in observation period definition, so did the numbers of individuals who satisfied eligibility criteria (Table 2). There were more patients eligible for SCCS analyses than for CCO analyses, with the number of control individuals far exceeding the number of DDI-exposed individuals across both designs. The controls were, on average, younger than DDI-exposed individuals.

Table 2.

Individuals eligible for each empirical example and study design

	CCO		SCCS
Example	Concomitant exposure	Controlsa	Concomitant exposure	Controlsa
Simvastatin-clarithromycin, N	123	1,146	304	13,616
Mean age, years (SD)	67.2 (13.2)	52.7 (15.7)	63.4 (12.9)	49.6 (15.9)
Males, N (%)	39 (31.7%)	278 (24.3%)	95 (31.3%)	3,488 (25.6%)
Atorvastatin-valsartan, N	790	4,518	776	9,558
Mean age, years (SD)	72.0 (12.7)	65.3 (14.8)	69.6 (13.1)	62.4 (15.3)
Males, N (%)	361 (45.7%)	1,381 (30.6%)	344 (44.3%)	3,192 (33.4%)
Dabigatran-clarithromycin, N	8	2,257	45	29,548
Mean age, years (SD)	72.5 (12.3)	58.4 (16.0)	77.2 (10.4)	55.2 (16.0)
Males, N (%)	3 (37.5%)	1,080 (47.9%)	23 (51.1%)	14,600 (49.4%)
Dabigatran-amiodarone, N	213	3,993	631	12,334
Mean age, years (SD)	75.7 (10.3)	76.3 (11.6)	75.0 (10.2)	70.6 (11.8)
Males, N (%)	119 (55.9%)	2,572 (64.4%)	356 (56.4%)	7,897 (64.0%)
Dabigatran-verapamil, N	57	5,191	116	10,129
Mean age, years (SD)	76.7 (9.6)	69.0 (14.1)	75.6 (10.2)	62.9 (15.4)
Males, N (%)	25 (43.9%)	2,173 (41.9%)	54 (46.6%)	4,217 (41.6%)

In case-crossover analyses, individuals only contribute to analysis if their exposure changes across the referent and hazard windows. In SCCS, individuals could have more than one observation period, which were evaluated independently. See Tables S5-S14 for N individuals contributing to CCO analyses and N observation periods in SCCS analyses.

CCO, case-crossover; SCCS, self-controlled case series.

^aControls were individuals not exposed to the object drug of interest and other drugs from the same therapeutic class (all statins in simvastatin and atorvastatin examples, and all oral anticoagulants in dabigatran examples).

The results for the main analysis of simvastatin-clarithromycin DDI were consistent between the two designs (Table 3), revealing increased risk associated with clarithromycin both among patients exposed to simvastatin and patients not exposed to statins (controls). The adjustment led to attenuation of the association with 95% confidence intervals (CI) overlapping the null. Sensitivity analyses (Figure 2; Tables S5 and S6) revealed sensitivity of CCO estimates to window specification with adjusted estimates moving from 1.29 (95% CI, 0.73–2.28) to 2.70 (95% CI, 1.42–5.13) and 4.03 (95% CI, 2.04–7.94) when hazard and referent windows were extended by 3 and 7 days, respectively. SCCS sensitivity analyses were consistent with findings from the main analysis.

Table 3.

CCO and SCCS results

	CCO			SCCS
Example/precipitant	Concomitant OR (95% CI)	Controlsa OR (95% CI)	Adjusted OR (95% CI)	Concomitant IR (95% CI)	Controla IR (95% CI)	Adjusted IR (95% CI)
Simvastatin, clarithromycin, and muscle-related toxicity
Clarithromycin	2.61 (1.52–4.50)	2.02 (1.71–2.38)	1.29 (0.73–2.28)	2.67 (1.82–3.91)	2.02 (1.82–2.24)	1.32 (0.89–1.96)
Atorvastatin, valsartan, and muscle-related toxicity
Valsartan	0.92 (0.75–1.12)	0.96 (0.89–1.05)	0.95 (0.77–1.19)	1.16 (0.91–1.48)	0.97 (0.91–1.02)	1.20 (0.94–1.55)
Dabigatran, P-gp inhibitors, and bleeding
Clarithromycin	–	1.86 (1.65–2.10)	–	2.48 (1.06–5.78)	2.06 (1.91–2.22)	1.20 (0.51–2.82)
Amiodarone	1.08 (0.74–1.56)	1.30 (1.20–1.42)	0.82 (0.56–1.21)	0.95 (0.74–1.21)	1.86 (1.77–1.95)	0.51 (0.40–0.66)
Verapamil	0.53 (0.25–1.13)	1.07 (1.00–1.16)	0.44 (0.20–0.98)	1.10 (0.54–2.22)	2.40 (2.29–2.52)	0.46 (0.22–0.93)

CCO, case-crossover; CI, confidence interval; IR, incidence ratio; OR, odds ratio; SCCS, self-controlled case series.

^aControls were individuals not exposed to the object drug of interest and other drugs from the same therapeutic class (all statins in simvastatin and atorvastatin examples, and all oral anticoagulants in dabigatran examples).

Figure 2.

Sensitivity analyses. Adjusted estimates are presented. For estimates in drug-drug interaction-exposed individuals and controls, see the Supplementary Material. *Hazard and referent (H/R) windows were extended to 17 days in the analyses of clarithromycin and 60 days in other analyses. **Hazard and referent windows were extended to 21 days in the analyses of clarithromycin and 90 days in other analyses. ***Washout period was extended from 30 days to 60 days in the analyses of chronic precipitants. ^¶Observation time in controls was limited to 180 days before and 180 days after the start of precipitant exposure; patients may have been censored earlier. SCCS, self-controlled case series.

In the atorvastatin-valsartan example, the adjusted CCO estimate was 0.95 (95% CI, 0.77–1.19) whereas the adjusted SCCS estimate was 1.20 (95% CI, 0.94–1.55). The difference in adjusted estimates was driven by the difference in estimates in DDI-exposed cases as the estimates from controls were almost identical between the two designs (Table 3). Sensitivity analyses and analyses stratified on atorvastatin dose yielded similar findings for both designs (Figure 2; Tables S7 and S8).

Due to the small number of individuals exposed to dabigatran and clarithromycin, we could not obtain an estimate for the dabigatran-clarithromycin DDI in CCO analyses. Extending the hazard and referent windows to 17 or 21 days yielded adjusted CCO estimates of 2.28 and 2.35, respectively, with wide 95% CI (Figure 2; Table S9). SCCS analyses yielded an adjusted estimate of 1.20 (95% CI, 0.51–2.82), which was attenuated in the sensitivity analysis with a 30-day washout (1.02, 95% CI, 0.43–2.44), but increased to 2.38 (95% CI, 1.02–5.57) when observation time was limited in controls (Table S10).

Both designs yielded no association between bleeding and amiodarone while on dabigatran but showed an association between amiodarone and bleeding in controls (Table 3). The association seen in controls persisted and increased through CCO sensitivity analyses (Table S11). Extending the washout to 30 days in SCCS analyses yielded findings that were similar to those observed in the main analysis; however, limiting observation time in controls yielded an incidence ratio (IR) of 0.68 (95% CI, 0.64–73) in controls and an adjusted IR of 1.38 (95% CI, 1.07–1.79; Figure 2, Table S12).

The CCO analyses of verapamil yielded estimates that varied widely across sensitivity analyses, primarily due to the small number of individuals exposed to dabigatran and verapamil (Table 3, Figure 2, Table S13). In SCCS analyses, exposure to verapamil in controls yielded an increased association that persisted across sensitivity analyses (Table S14), leading to a protective adjusted estimate (IR, 0.46, 95% CI, 0.22–0.93), which was slightly attenuated in sensitivity analyses (Table S14).

The evaluation of event-to-censoring times in SCCS analyses revealed that at least 30% and, in some examples, up to 60% of DDI-exposed individuals were censored within 30 days following an event, whereas 13% or fewer controls were censored during the same time window (Table S15). Evaluation of the distribution of precipitant drug dispensing revealed changes in exposure before and after the outcome across most examples (Figures S1-S5).

DISCUSSION

We implemented two of the most commonly used self-controlled designs, the unidirectional CCO and the bidirectional self-controlled case series, for identifying and quantifying health outcomes of DDIs in RWD. Overall, we observed similar findings between the two designs across five empirical examples, with the SCCS displaying better statistical efficiency. Notably, the bias adjustment via a control group had a larger impact on the results than the choice of design, and both designs displayed substantial variability across sensitivity analyses in at least some examples.

Self-controlled designs that compare individuals to themselves offer an attractive design choice for RWD DDI evaluation due to their inherent control for confounding by stable risk factors, including those that are not available in real-world databases or are measured imprecisely.¹⁰ Yet, these designs are still prone to bias. Self-controlled studies require and evaluate changes in drug therapy, which, in clinical practice, are often driven by changes in patient health status, leading to the possibility of time-varying, within-person confounding.^10,26 Both the CCO and the SCCS designs are susceptible to bias due to time-varying confounding, which, we believe, was the primary reason for spurious results we observed in controls across most of the examples we evaluated.

Bias in self-controlled designs can come not only from time-varying confounding, but also from the violations of other assumptions required for valid causal inference. For example, the unidirectional CCO, as traditionally implemented in evaluation of drug outcomes, requires stable exposure probability across the hazard and referent windows in the absence of drug effect.^14,29 The SCCS design requires no outcome-related changes in drug therapy and no outcome-related censoring.^14,30 Both designs require specification of the time at risk and of referent time during which outcomes could not be attributed to exposure. Because we largely obtained similar estimates from the two designs, the violation of these assumptions may represent a lesser threat to validity in DDI RWE studies as opposed to time-varying confounding, which is in line with prior findings from simulation studies.^14,30 However, bias due to violation of design-specific assumptions may still exist. In two of five examples we evaluated, more than half of DDI-exposed patients were censored within a month of outcome, suggesting substantial event-dependent censoring. In almost all examples, we observed changes in exposure following an outcome, suggesting event-dependent changes in exposure. At least two evaluated precipitant drugs (valsartan and verapamil) represent chronic therapies that may lead to bias in CCO analyses if most patients persist on therapy until they die.³¹ Our analyses of dabigatran examples showed that these biases may operate in opposite directions, leading to opposite estimates across sensitivity analyses.

To control for time-varying confounding, as well as for bias due to violations of design-specific assumptions, researchers often utilize a control group.^1,7,32 The validity of the adjustment relies on the assumption that bias observed in the analysis of controls approximates the bias present in the analysis of DDI-exposed cases. In our investigation, controls were individuals not exposed to the object drug of interest or other drugs from the same therapeutic class. Other approaches include selecting individuals on a drug that is known not to interact with the precipitant of interest (negative object drug) as controls.^1,8 There are advantages and limitations to either approach,^33,34 and a control group exposed to a negative object drug may be preferred in a SCCS study as it is more likely to produce observation time of comparable duration across DDI-exposed cases and controls. Longer observation periods may increase the probability and magnitude of time-varying confounding, which, we believe, was the primary source of bias we observed in SCCS analyses of verapamil and amiodarone in controls. Limiting the observation time moved the estimates closer to the null, and, possibly, closer to approximating bias in DDI-exposed cases. In CCO analyses, where observation time is fixed and is identical across DDI-exposed individuals and controls, this advantage of a negative object drug is of less relevance. Ultimately, with either approach and either design, if bias is differential across DDI-exposed and control groups, final estimates will still be biased, as was indicated by protective adjusted estimates we obtained in the analyses of dabigatran-amiodarone and dabigatran-verapamil interactions. Additional adjustment for time-varying confounding at the analysis stage is possible and is often implemented in both the CCO and the SCCS; however, if time-varying confounders are affected by treatment, including them in the same model with exposure can result in bias.^4,35

Both the CCO and the SCCS are also subject to the usual limitations of RWD DDI evaluations. RWD-based studies are restricted to outcomes that can be accurately measured in the data available.⁴ Healthcare claims are reliable sources of pharmacy dispensing; however, there is no information on how and when individuals take dispensed medications. In situations of a suspected DDI, patients may be instructed to stop or reduce the dose of object drug therapy, leading to exposure misclassification in RWD analyses. Moreover, if managed well, DDIs may not result in serious adverse events and may not produce evidence of adverse health outcomes in RWD analyses. Finally, if interacting drugs are avoided in clinical practice, analyses of large databases may still be underpowered and result in unstable estimates due to the small numbers of DDI-exposed individuals. These limitations should be kept in mind when interpreting any RWE on DDIs, particularly those that are well known.

In addition, it should be kept in mind that we evaluated only five empirical examples, and it is possible that in some scenarios not considered, the CCO and the SCCS designs would produce drastically different findings. It may be advisable to implement both designs to ensure the robustness of findings; although bias due to time-varying confounding may persist across both designs. Whereas we aimed to be consistent between the two designs, some decisions, such as precipitant drug exposure definition (based on dispensing in CCO and days’ supply in the SCCS), were different. Ultimately, we implemented the designs as they are commonly implemented in evaluations of drug outcomes in RWD and cannot exclude that some of the differences we observed were driven by differences in definitions, as opposed to bias due to violation of design-specific assumptions.

Despite these limitations, our results offer important insights into how self-controlled designs can be implemented for generating RWE for DDIs. Although the ability of self-controlled designs to estimate causal parameters has been questioned,³⁶ we believe that they may produce useful information in specific clinical scenarios or applications. For example, our results and other recent RWD analyses have demonstrated the ability of self-controlled designs to identify known DDIs.⁷ As the role of RWE in DDI research continues to expand, future studies should seek to understand when and how different study designs and analytic approaches can approximate causal parameters of interest.

In conclusion, although self-controlled designs offer an attractive alternative to other observational study designs for evaluating outcomes of DDIs due to their inherent ability to control for time-stable confounders, time-varying confounding poses substantial threat to their validity. A control group may ameliorate some of the bias but adjusted estimates may still be biased if the mechanism and magnitude of bias is differential across DDI-exposed and control individuals. The choice of a control group may have bigger impact on final estimates than the choice of a specific self-controlled design.

Study Highlights.

WHAT IS THE CURRENT KNOWLEDGE ON THE TOPIC?

The case-crossover (CCO) and the self-controlled case series, two major designs that have been implemented in real-world evidence (RWE) research on drug-drug interactions (DDIs), share some characteristics, but also have design-specific advantages and limitations.

WHAT QUESTION DID THIS STUDY ADDRESS?

This study compared the unidirectional CCO and bidirectional self-controlled case series designs in the context of evaluating clinical outcomes of DDIs using real-world data.

WHAT DOES THIS STUDY ADD TO OUR KNOWLEDGE?

In five empirical examples, the use of a control group, which was implemented to control for time-varying confounding, had a bigger impact on final estimates than the choice of a specific self-controlled design.

HOW MIGHT THIS CHANGE CLINICAL PHARMACOLOGY OR TRANSLATIONAL SCIENCE?

Both self-controlled designs are susceptible to bias due to time-varying, within-person confounding. Whereas the use of a control group may ameliorate this bias, residual bias and overadjustment are possible. Care should be taken when implementing and interpreting RWE studies of DDIs.