126.96.36.199 Pragmatic trials
RCTs are considered the gold standard for demonstrating the efficacy of medicinal products and for obtaining an initial estimate of the risk of adverse outcomes. However, they are not necessarily indicative of the benefits, risks or comparative effectiveness of an intervention when used in clinical practice. The IMI GetReal Glossary defines a pragmatic clinical trial (PCT) as ‘a study comparing several health interventions among a randomised, diverse population representing clinical practice, and measuring a broad range of health outcomes’. The publication Series: Pragmatic trials and real world evidence: Paper 1. Introduction (J Clin Epidemiol. 2017;88:7-13) describes the main characteristics of this design and the complex interplay between design options, feasibility, acceptability, validity, precision, and generalisability of the results, and the review Pragmatic Trials (N Engl J Med. 2016;375(5):454-63) discusses the context in which a pragmatic design is relevant, and its strengths and limitations based on examples.
PCTs are focused on evaluating benefits and risks of treatments in patient populations and settings that are more representative of routine clinical practice. To ensure generalisability, PCTs should represent the patients to whom the treatment will be applied, for instance, inclusion criteria may be broader (e.g., allowing co-morbidity, co-medication, wider age range) and the follow-up may be minimised and allow for treatment switching. Real-World Data and Randomised Controlled Trials: The Salford Lung Study (Adv Ther. 2020;37(3):977-997) and Monitoring safety in a phase III real-world effectiveness trial: use of novel methodology in the Salford Lung Study (Pharmacoepidemiol Drug Saf. 2017;26(3):344-352) describes the model of a phase III PCT where patients were enrolled through primary care practices using minimal exclusion criteria and without extensive diagnostic testing, and where potential safety events were captured through patients’ electronic health records and triggered review by the specialist safety team.
Pragmatic explanatory continuum summary (PRECIS): a tool to help trial designers (CMAJ. 2009;180(10): E45-E57) is a tool to support pragmatic trial designs and help define and evaluate the degree of pragmatism. The Pragmatic–Explanatory Continuum Indicator Summary (PRECIS) tool has been further refined and now comprises nine domains each scored on a 5 point Likert scale ranging from very explanatory to very pragmatic with an exclusive focus on the issue of applicability (The PRECIS-2 tool: designing trials that are fit for purpose. BMJ. 2015;350: h2147). A checklist and additional guidance is provided in Improving the reporting of pragmatic trials: an extension of the CONSORT statement (BMJ. 2008;337 (a2390):1-8), and Good Clinical Practice Guidance and Pragmatic Clinical Trials: Balancing the Best of Both Worlds (Circulation 2016;133(9):872-80) discusses the application of Good Clinical Practice to pragmatic trials, and the use of additional data sources such as registries and electronic health records for “EHR-facilitated” PCTs.
Based on the evidence that the current costs and complexity of conducting randomised trials lead to more restrictive eligibility criteria and shorter durations of trials, and therefore reduce the generalisability and reliability of the evidence about the efficacy and safety of interventions, the article The Magic of Randomization versus the Myth of Real-World Evidence (N Engl J Med. 2020;382(7):674-678) proposes measures to remove practical obstacles to the conduct of randomised trials of appropriate size.
The BRACE CORONA study (Effect of Discontinuing vs Continuing Angiotensin-Converting Enzyme Inhibitors and Angiotensin II Receptor Blockers on Days Alive and Out of the Hospital in Patients Admitted With COVID-19: A Randomized Clinical Trial, JAMA. 2021;325(3):254-64) is a registry-based pragmatic trial that included patients hospitalised with COVID-19 who were taking ACEIs or ARBs prior to hospital admission, to determine whether discontinuation vs. continuation of these drugs affects the number of days alive and out of the hospital. Patients with a suspected COVID-19 diagnosis were included in the registry and followed up until diagnosis confirmation and randomised to either discontinue or continue ACEI or ARB therapy for 30 days. There was no specific treatment modification beyond discontinuing or continuing use of ACEIs or ARBs, the study team provided oversight on drug replacement based on current treatment guidelines. Treatment adherence was assessed based on medical prescriptions recorded in electronic health records after discharge.
188.8.131.52 Large simple trials
Large simple trials are pragmatic clinical trials with minimal data collection narrowly focused on clearly defined outcomes important to patients as well as clinicians. Their large sample size provides adequate statistical power to detect even small differences in effects, the clinical relevance of which can subsequently be assessed. Additionally, large simple trials include a follow-up time that mimics routine clinical practice.
Large simple trials are particularly suited when an adverse event is very rare or has a delayed latency (with a large expected attrition rate), when the population exposed to the risk is heterogeneous (e.g., different indications and age groups), when several risks need to be assessed in the same trial or when many confounding factors need to be balanced between treatment groups. In these circumstances, the cost and complexity of a traditional RCT may outweigh its advantages and large simple trials can help keep the volume and complexity of data collection to a minimum.
Outcomes that are simple and objective can also be measured from the routine process of care using epidemiological follow-up methods, for example by using questionnaires or hospital discharge records. Classical examples of published large simple trials are An assessment of the safety of paediatric ibuprofen: a practitioner based randomised clinical trial (JAMA. 1995;279:929-33) and Comparative mortality associated with ziprasidone and olanzapine in real-world use among 18,154 patients with schizophrenia: The Zodiac Observational Study of Cardiac Outcomes (ZODIAC) (Am J Psychiatry 2011;168(2):193-201).
Note that the use of the term ‘simple’ in the expression ‘Large simple trials’ refers to data structure and not to data collection. It is used in relation to situations in which a small number of outcomes are measured. The term may therefore not adequately reflect the complexity of the studies undertaken.
184.108.40.206 Randomised database studies
Randomised database studies can be considered a special form of a large simple trial where patients included in the trial are enrolled from a healthcare system with electronic records. Eligible patients may be identified and flagged automatically by the software, with the opportunity of allowing comparison of included and non-included patients with respect to demographic characteristics and clinical history. Database screening or record linkage can be used to collect outcomes of interest otherwise assessed through the normal process of care. Patient recruitment, informed consent and proper documentation of patient information are hurdles that still need to be addressed in accordance with the applicable legislation for RCTs.
Randomised database studies attempt to combine the advantages of randomisation and observational database studies. These and other aspects of randomised database studies are discussed in The opportunities and challenges of pragmatic point-of-care randomised trials using routinely collected electronic records: evaluations of two exemplar trials (Health Technol Assess. 2014;18(43):1-146) which illustrates the practical implementation of randomised studies in general practice databases. More recent work has been conducted to extend quality standards in the Consolidated Standards of Reporting Trials (CONSORT) to also include database studies: CONSORT extension for the reporting of randomised controlled trials conducted using cohorts and routinely collected data (CONSORT-ROUTINE): checklist with explanation and elaboration (BMJ. 2021;373:n857). These quality standards for reporting also have implications on trial design and conduct.
Published examples of randomised database studies are still scarce, however, this design is becoming more common with the increasing use of electronic health records. Pragmatic randomised trials using routine electronic health records: putting them to the test (BMJ. 2012;344:e55) describes a project to implement randomised trials in the everyday clinical work of general practitioners, comparing treatments that are already in common use, and using routinely collected electronic healthcare records both to identify participants and to gather results. The above-mentioned Salford Lung Study, and the study described in Design of a pragmatic clinical trial embedded in the Electronic Health Record: The VA's Diuretic Comparison Project (Contemp Clin Trials 2022, 116:106754) belong to this category.
A particular form of randomised database studies is the registry-based randomised trial, which uses an existing registry as a source for the identification of cases, their randomisation and their follow-up. The editorial The randomized registry trial - the next disruptive technology in clinical research? (N Engl J Med. 2013;369(17):1579-81) introduces this concept. This hybrid design aims at achieving both internal and external validity by performing a RCT in a data source with higher generalisability (such as registries). Other examples are the TASTE trial that followed patients in the long-term using data from a Scandinavian registry (Thrombus aspiration during ST-segment elevation myocardial infarction (N Engl J Med. 2013;369:1587-97) and A registry-based randomized trial comparing radial and femoral approaches in women undergoing percutaneous coronary intervention: the SAFE-PCI for Women (Study of Access Site for Enhancement of PCI for Women) trial (JACC Cardiovasc Interv. 2014;7:857-67).
The importance of large simple trials has been highlighted by their role in evaluating well-established products that were repurposed for the treatment of COVID-19. The PRINCIPLE Trial platform (for trials in primary care) and the RECOVERY Trial platform (for trials in hospitals) have been recruiting large numbers of study participants and sites within short periods of time. In addition to brief case report forms, important clinical outcomes such as death, intensive care admission and ventilation were ascertained through data linkage to existing data streams. The study Lopinavir-ritonavir in patients admitted to hospital with COVID-19 (RECOVERY): a randomised, controlled, open-label, platform trial (Lancet 2020;396:1345–52) found that in patients admitted to hospital with COVID-19, lopinavir–ritonavir was not associated with reductions in 28-day mortality, duration of hospital stay, or risk of progressing to invasive mechanical ventilation or death. On the other hand, in Dexamethasone in Hospitalized Patients with Covid-19 (N Engl J Med. 2021;384(8):693-704), the RECOVERY trial also reported that the use of dexamethasone resulted in lower 28-day mortality in patients who were receiving either invasive mechanical ventilation or oxygen alone at randomisation. Inhaled budesonide for COVID-19 in people at high risk of complications in the community in the UK (PRINCIPLE): a randomised, controlled, open-label, adaptive platform trial (Lancet 2021;398:843-55) reported on the effectiveness of an inhaled corticosteroid for COVID-19 community patients. The streamlined and reusable approaches in data collection in these still recruiting platform trials clearly were essential in the achievements to enrol larger numbers of trial participants and evaluate multiple treatments rapidly.
Observational emulation of a clinical trial was initially introduced in The clinical trial as a paradigm for epidemiologic research (J Clin Epidemiol. 1989;42(6):491-6). It was later extended to pharmacoepidemiology as a conceptual framework helping researchers to identify and avoid potential biases, as described in Using Big Data to Emulate a Target Trial When a Randomized Trial Is Not Available (Am J Epidemiol. 2016;183(8):758-64). The number of target trial emulations using observational data published in the scientific literature is now rapidly growing.
The underlying idea is to design a hypothetical ideal randomised trial (“target trial”) that would answer the research question. The target trial is described with regards to all design elements: the eligibility criteria, the treatment strategies, the assignment procedure, the follow-up, the outcome, the causal contrasts and the analysis plan. In the second step, the researcher specifies how best to emulate the design elements of the target trial using the available observational data source and what analytic approaches to take given the trade-offs in an observational setting. The target trial paradigm aims to prevent some common biases, such as immortal time bias or prevalent user bias while also identifying situations where adequate emulation may not be possible using the data at hand. It also facilitates a systematic methodological evaluation and comparison of observational studies (Specifying a target trial prevents immortal time bias and other self-inflicted injuries in observational analyses. J Clin Epidemiol. 2016;79:70-5).The framework can also be used to help describe the randomised trial which the available observational data can most closely emulate.
Several studies have compared the results of randomised clinical trials and of observational target trial emulations designed to ask similar questions. Comparing Effect Estimates in Randomized Trials and Observational Studies From the Same Population: An Application to Percutaneous Coronary Intervention (J Am Hear Assoc. 2021;10:e020357) highlighted differences between the two study designs that may affect the results and be generalisable to other types of interventions: the observational study conducted in the same registry used to recruit clinical trial patients needed to be performed in a period that precedes the clinical trial; eligibility criteria differed as not all the necessary data were available for the study and no exclusion was based on informed consent; some outcomes could not be defined similarly; and some potential confounding factors could not be measured. Emulating a target trial in case-control designs: an application to statins and colorectal cancer (Int J Epidemiol. 2020;49(5):1637–46) describes how to emulate a target trial using case-control data and demonstrates that better emulation reduces the discrepancies between observational and randomised trial evidence. Interim results from the 10 first emulations reported in Emulating Randomized Clinical Trials With Nonrandomized Real-World Evidence Studies: First Results From the RCT DUPLICATE Initiative (Circulation 2021;143(10):1002-13) found that selection of active comparator therapies with similar indications and use patterns enhances the validity of real-world evidence. Emulation differences versus biases when calibrating RWE findings against RCTs (Clin Pharmacol Ther. 2020;107(4):735-7) provided guidance on how to investigate and interpret differences in treatment effect estimates from the two study types. The authors of these articles also emphasise that emulation of clinical trials is not the purpose of observational studies. Their strength is the ability to answer questions that cannot be answered by RCTs, as in cases where randomisation would be difficult or unethical or questions cannot be answered by RCTs, and synergies between the two designs should be further explored to support faster availability of trial results into clinical practice.
Successful emulation of a target trial requires proper definition of time points, including time zero of follow-up in the observational data. Using Big Data to Emulate a Target Trial When a Randomized Trial Is Not Available (Am J Epidemiol. 2016;183(8) 758-64) describes two unbiased choices of time zero when eligibility criteria can be met at multiple times. Studies on the effect of treatment duration are also often impaired by selection bias and How to estimate the effect of treatment duration on survival outcomes using observational data (BMJ. 2018;360: k182) proposes a 3-step method (cloning, censoring, weighting) for overcoming bias in these types of studies.
In the context of the COVID-19 pandemic, several observational studies on vaccine effectiveness used target trial emulation. The observational study BNT162b2 mRNA Covid-19 Vaccine in a Nationwide Mass Vaccination Setting (N Engl J Med. 2021;384(15):1412-23) emulated a target trial of the effect of the BNT162b2 vaccine on COVID-19 outcomes by matching vaccine recipients and controls on a daily basis on a wide range of potential confounding factors. The large population size of four large health care organisations led to a nearly perfect matching leading to a consistent pattern of similarity between the groups in the days just before day 12 after the first dose, the anticipated onset of the vaccine effect. A similar target trial emulation design was used in Comparative Effectiveness of BNT162b2 and mRNA-1273 Vaccines in U.S. Veterans (N Engl J Med. 2022;386(2):105-15).
ROBINS-I: a tool for assessing risk of bias in non-randomised studies of interventions (BMJ. 2016;355:i4919) supports the evaluation of bias in estimates of the comparative effectiveness (harm or benefit) of interventions from studies that did not use randomisation and can be applied to target trials and to systematic reviews that include non-randomised studies.
Statistical aspects of target trials are discussed in Chapters 3.6 (The target trial) and 22 (Target trial emulation) of the Causal Inference Book (Hernán MA, Robins JM (2020). Causal Inference: What If. Boca Raton: Chapman & Hall/CRC).
The self-controlled case series (SCCS) design was initially developed for vaccines (see Chapter 15.2). It is a case-only design where the observation period for each case is divided into risk window(s) (e.g., number of days following a vaccine or prescription exposure) and control window(s) (observed time before and after risk windows). SCCS estimates a relative incidence, that is, incidence rates within the risk window(s) after exposure relative to incidence rates within the control window(s). The SCCS design inherently controls for time-invariant and between-individual confounding, but potential confounders that vary over time within the same persons still need to be controlled for.
Three assumptions of the SCCS are that 1) events arise independently within individuals (e.g., fractures do not affect the occurrence of a subsequent fracture), 2) events do not influence subsequent follow-up, and 3) the event itself does not affect the chance of being exposed. However, SCCS studies can be adapted to circumvent these assumptions in specific situations. The third assumption is generally the most limiting, but where the event only temporarily affects the chance of exposure, additional ‘pre-exposure’ windows can be included; otherwise Cases series analysis for censored, perturbed, or curtailed post-event exposures (Biostatistics 2009;10(1):3-16) describes an extended SCCS method that can address permanent changes to the chance of exposure post-event where exposure windows are short, and is suitable where the event of interest is death.
A general introduction is given in Self controlled case series methods: an alternative to standard epidemiological study designs (BMJ. 2016; 354), and in Tutorial in biostatistics: the self-controlled case series method (Stat Med. 2006;25(10):1768-97), which further explains how to fit SCCS models using standard statistical packages. The book Self-Controlled Case Series Studies: A Modelling Guide with R (P. Farrington, H. Whitaker, Y. G. Weldeselassie, 1st Edition, Chapman and Hall/CRC, 2021) provides a more detailed account. Examples from the tutorial and book are available from http://sccs-studies.info/.
An illustrative example of an SCCS study is Opioids and the Risk of Fracture: a Self-Controlled Case Series Study in the Clinical Practice Research Datalink (Am J Epidemiol. 2021;190(7):1324-31) where the relative incidence of fracture was estimated by comparing time windows when cases were exposed following an opioid prescription and unexposed to opioids. Multiple contiguous risk windows were included to capture changes in risk from new use through to long-term use. A washout window was included after prescriptions stopped, and a pre-exposure window was included to address potential bias from event-dependent exposure. Age, season and exposure to fracture risk–increasing drugs were adjusted for. SCCS assumptions were checked using sensitivity analyses, including taking first fractures only to address independence of events, and excluding individuals who died to address events influencing follow-up.
Use of the self-controlled case-series method in vaccine safety studies: review and recommendations for best practice (Epidemiol Infect. 2011;139(12):1805-17) assesses how the SCCS method has been used across 40 vaccine studies, highlights good practice and gives guidance on how the method should be used and reported. Using several methods of analysis is recommended, as it can reinforce conclusions or shed light on possible sources of bias when these differ for different study designs. When should case-only designs be used for safety monitoring of medical products? (Pharmacoepidemiol Drug Saf 2012;21(Suppl. 1):50-61) compares the SCCS and case-crossover methods as to their use, strengths, and major differences (directionality). It concludes that case-only analyses of intermittent users complement the cohort analyses of prolonged users because their different biases compensate for one another. It also provides recommendations on when case-only designs should and should not be used for drug safety monitoring. Empirical performance of the self-controlled case series design: lessons for developing a risk identification and analysis system (Drug Saf. 2013;36(Suppl. 1):S83-S93) evaluates the performance of the SCCS design using 399 drug-health outcome pairs in 5 observational databases and 6 simulated datasets. Four outcomes and five design choices were assessed. The Use of active Comparators in self-controlled Designs (Am J Epidemiol. 2021;190(10):2181-7) showed that presence of confounding by indication can be mitigated by using an active comparator, using an empirical example of a study of the association between penicillin and venous thromboembolism (VTE), with roxithromycin, a macrolide antibiotic, as the comparator, and upper respiratory infection, a transient risk factor for VTE, representing time-dependent confounding by indication.
The self-controlled risk interval design (SCRI) has been mostly used in vaccine safety studies. It is a restricted SCCS design suitable when exposure risk windows are short. Rather than using all follow-up time available, short control windows before and/or after risk windows are selected; gaps between risk and control windows may be included e.g., to allow for washout. Power is reduced as compared with the SCCS, but will often suffice for use with large databases where events are not very rare. Since each individual’s observation period is short, age and time effects often do not require control. In Use of FDA's Sentinel System to Quantify Seizure Risk Immediately Following New Ranolazine Exposure (Drug Saf. 2019;42(7):897-906), new users were restricted to patients with 32 days of continuous exposure to ranolazine (i.e., capturing individuals that typically would have a 30-day dispensing). The observation period began the day after the start of the incident ranolazine dispensing and ended on the 32nd day after the index date, with two risk windows covering days 1-10 and 11-20, and the control window days 21-32. The relative incidence is calculated as a ratio of the number of events in the risk interval to the number of events in the control interval multiplied by the ratio of the length of control interval to length of risk interval from only cases.
According to the Master Protocol: Assessment of Risk of Safety Outcomes Following COVID-19 Vaccination (bestinitiative.org), the standard SCCS design is more adaptable and is thus preferred when risk or control windows may be less well-defined, when there is a need to increase statistical power, or when unmeasured time-varying confounding is a lesser concern. The SCCS design can also be more easily used to assess multiple occurrences of independent events within an individual. The SCRI design is preferred when it is feasible to have strictly defined risk and control windows for outcomes of interest, or when time varying confounding is a concern. Despite the short observation periods, SCRI may be vulnerable to time-varying confounders; a means of adjustment in SCRI studies, e.g., for steep age effects sometimes seen in studies of childhood vaccine safety, is provided in Quantifying the impact of time-varying baseline risk adjustment in the self-controlled risk interval design (Pharmacoepidemiol Drug Saf. 2015; 24(12):1304-12).
The validity of causal associations may be tested by using control exposures or outcomes. A negative control outcome is a variable known not to be causally affected by the treatment of interest. Likewise, a negative control exposure is a variable known not to causally affect the outcome of interest. Conversely, a positive control outcome is a variable that is understood to be positively associated with the exposure of interest and a positive control exposure is one which is known to increase the risk of the outcome of interest.
Well-selected positive and negative controls support decision-making on whether the data at hand correctly support the study results for known associations or correctly demonstrate lack of association. Positive controls with negative findings and negative controls with positive findings may signal the presence of bias, as illustrated in a study showing that adherence to statins was associated with a decreased risk of biologically implausible outcomes (Statin adherence and risk of accidents: a cautionary tale, Circulation 2009;119(15):2051-7) and in Utilization of Positive and Negative Controls to Examine Comorbid Associations in Observational Database Studies (Med Care 2017;55(3):244-51). This general principle, with additional examples, is described in Control Outcomes and Exposures for Improving Internal Validity of Nonrandomized Studies (Health Serv Res. 2015;50(5):1432-51) and Negative Controls: A Tool for Detecting Confounding and Bias in Observational Studies (Epidemiology 2010 May; 21(3): 383–388.). Negative controls have also been used to identify other sources of bias including selection bias and measurement bias in Brief Report: Negative Controls to Detect Selection Bias and Measurement Bias in Epidemiologic Studies (Epidemiology. 2016 Sep; 27(5): 637–641) and in Negative control exposure studies in the presence of measurement error: implications for attempted effect estimate calibration (Int J Epidemiol. 2018 Apr; 47(2): 587–596). Chapter 18. Method Validity of The Book of OHDSI (2021) recommends use of negative and positive controls as a diagnostic test to evaluate whether the study design produced valid results and proposes practical considerations for their selection. Selecting drug-event combinations as reliable controls nevertheless poses important challenges: it is difficult to establish for negative controls proof of absence of an association, and it is still more problematic to select positive controls because it is desirable not only to measure an association but also an accurate estimate of the effect size. This has led to attempts to establish libraries of controls that can be used to characterise the performance of different observational datasets in detecting various types of associations using a number of different study designs. Although the methods used to identify negative and positive controls may be questioned according to Evidence of Misclassification of Drug-Event Associations Classified as Gold Standard 'Negative Controls' by the Observational Medical Outcomes Partnership (OMOP) (Drug Saf. 2016;39(5):421-32), this approach may allow to separate random and systematic errors in epidemiological studies, providing a context for evaluating uncertainty surrounding effect estimates.
Beyond the detection of bias, positive and negative controls can be used to correct unmeasured confounding as described in Interpreting observational studies: Why empirical calibration is needed to correct p-values (Stat Med. 2014;33(2):209-18), Robust empirical calibration of p-values using observational data (Stat Med. 2016;35(22):3883-8), Empirical confidence interval calibration for population-level effect estimation studies in observational healthcare data (Proc Natl Acad Sci. USA 2018;115(11): 571-7), Empirical assessment of case-based methods for identification of drugs associated with acute liver injury in the French National Healthcare System database (SNDS) (Pharmacoepidemiol Drug Saf. 2021;30(3):320-33), and Risk of depression, suicide and psychosis with hydroxychloroquine treatment for rheumatoid arthritis: a multinational network cohort study (Rheumatology (Oxford) 2021;60:3222-34). However, Limitations of empirical calibration of p-values using observational data, Stat Med. 2016;35(22):3869-82) concludes that, although the method may reduce the number of false positive results, it may also reduce the ability to detect a true safety or efficacy signal.
The main purpose of using an active comparator is to reduce confounding by indication or by severity. Its use is optimal in the context of the new user design (see Chapter 5.1.1), whereby comparison is between patients with the same indication initiating different treatments as described in The active comparator, new user study design in pharmacoepidemiology: historical foundations and contemporary application, Curr Epidemiol Rep. 2015;2(4):221-8. For example, the study Risk of skin cancer in new users of thiazides and thiazide-like diuretics: a cohort study using an active comparator group (Br J Dermatol. 2021;185:343-52) used a cohort design with stratification on the propensity score to control for baseline covariates to estimate incidence rates and incidence rate ratios in short-term (<20 prescriptions) and long-term (≥20 prescriptions) drug users. Active-comparator design and new-user design in observational studies (Nat Rev Rheumatol. 2015;11:437-41) summarises the three main advantages of active comparator design: to increase the similarity in measured patient characteristics between treatment groups; to reduce potential for unmeasured confounding; and possibly to improve the clinical relevance of the research question.
Ideally, an active comparator should be chosen to represent the counterfactual risk of a given outcome with a different treatment, i.e., it should have a known and positive safety profile with respect to the event(s) of interest and ideally represent the background risk in the diseased (for example, safety of antiepileptics in pregnancy in relation to risk of congenital malformations could be compared against that of lamotrigine, which is known not to be teratogenic).
With newly marketed medicines, an active comparator with ideal comparability of patients’ characteristics may be unavailable because prescribing of newly marketed medicines may be driven to a greater extent by patients’ prognostic characteristics (early users may be either sicker or healthier than all patients with the indication) and by reimbursement considerations compared to prescribing of established medicines. This is described for comparative effectiveness studies in Assessing the comparative effectiveness of newly marketed medications: methodological challenges and implications for drug development (Clin Pharmacol Ther. 2011;90(6):777-90) and in Newly marketed medications present unique challenges for nonrandomized comparative effectiveness analyses. (J Comp Eff Res. 2012;1(2):109-11). Other challenges include treatment effect heterogeneity as patient characteristics of users evolve over time, and low precision owing to slow drug uptake.
In evaluating the effectiveness of population-level interventions that are implemented at a specific point in time (with clearly defined before-after periods, such as policy effect date, regulatory action date) interrupted time series (ITS) studies are becoming the standard approach. ITS, a quasi-experimental design with which to evaluate the longitudinal effects of interventions, through regression modelling, establishes the expected pre-intervention trend for an outcome of interest. The counterfactual scenario in the absence of the intervention serves as the comparator, the expected trend that provides a comparison for the evaluation of the impact of the intervention by examining any change occurring following the intervention period (Interrupted time series regression for the evaluation of public health interventions: a tutorial, Int J Epidemiol. 2017;46:348-55).
ITS analysis requires that several assumptions are met, its implementation is technically sophisticated, as explained in Regression based quasi-experimental approach when randomisation is not an option: Interrupted time series analysis (BMJ. 2015; 350:h2750). The use of ITS regression in impact research is illustrated in Chapter 15.4, Methods for pharmacovigilance impact research.
When data on exposed and control populations is available, Difference-in-Differences (DiD) methods are sometimes preferable. These methods compare the outcome mean or trend for exposed and control groups before and after a certain time point, providing insight into the changes of the variable for the exposed population relative to the change in the negative outcome group. This approach can be a more robust approach to causal inference than ITS, by comparing the exposed group to a control group subject to the same time-varying factors. First, DiD takes the difference for both groups before and after the intervention. Then it subtracts the difference of the control group from the exposed group to control for time-varying factors, thus estimating the clean impact of the intervention.
A basic introduction on the method can be found in Impact evaluation using Difference-in-Differences (RAUSP Management Journal 2019;54:519-532). Further extensions can be found in the literature, for example assessment of variation in treatment timing, as in Difference-in-differences with variation in treatment timing (Journal of Econometrics 2021;225:254-77). A good overview of the method applied to public health policy research is available in Designing Difference in Difference Studies: Best Practices for Public Health Policy Research (Annu Rev Public Health 2018;39:53-469).
Note: Chapter 4.4.7. has not been updated for Revision 10
Case-population studies are a form of ecological studies where cases are compared to an aggregated comparator consisting of population data. The case-population study design: an analysis of its application in pharmacovigilance (Drug Saf. 2011;34(10):861-8) explains its design and its application in pharmacovigilance for signal generation and drug surveillance. The design is also explained in Chapter 2: Study designs in drug utilization research of the textbook Drug Utilization Research - Methods and Applications (M Elseviers, B Wettermark, AB Almarsdóttir, et al. Editors. Wiley Blackwell, 2016). An example is a multinational case-population study aiming to estimate population rates of a suspected adverse event using national sales data in Transplantation for Acute Liver Failure in Patients Exposed to NSAIDs or Paracetamol, Drug Saf. 2013;36(2):135–44. Based on the same study, Choice of the denominator in case population studies: event rates for registration for liver transplantation after exposure to NSAIDs in the SALT study in France (Pharmacoepidemiol Drug Saf. 2013;22(2):160-7) compared sales data and healthcare insurance data as denominators to estimate population exposure and found large differences in the event rates. Choosing the wrong denominator in case-population studies might generate erroneous results. The choice of the right denominator depends not only on a valid data source but will also depend on the hazard function of the adverse event.
The case-population approach has also been adapted for vaccine safety surveillance, in particular for prospective investigation of urgent vaccine safety concerns or for the prospective generation of vaccine safety signals (see Vaccine Case-Population: A New Method for Vaccine Safety Surveillance, Drug Saf. 2016 Dec;39(12):1197-1209).
Use of the case-population design for fast investigation is illustrated in Use of renin-angiotensin-aldosterone system inhibitors and risk of COVID-19 requiring admission to hospital: a case-population study (Lancet 2020;395(10238):1705-14), in which the authors consecutively selected patients aged 18 years or older with a PCR-confirmed diagnosis of COVID-19 requiring admission to hospital from seven hospitals between March 1 and March 24, 2020. As a reference group, ten patients per case were randomly sampled, individually matched for age, sex, region and date of admission to hospital from a primary health-care database (available year: 2018). Information was extracted on comorbidities and prescriptions up to the month before index date from electronic clinical records of both cases and controls. Although the cases and controls originated from different data sources in different years, it was assumed that the primary health-care database of controls represented the source population of the cases and that a random sample of controls from that database would provide a valid estimate of the prevalence of the exposure and covariates in the source population, approaching the primary base paradigm of case-control studies.
A pragmatic attitude towards case-population studies is recommended: in situations where nation-wide or region-wide electronic health records (EHRs) are available and allow assessing the outcomes and confounders with sufficient validity, a case-population approach is neither necessary nor desirable, as one can perform a population-based cohort or case-control study with adequate control for confounding. In situations where outcomes are difficult to ascertain in EHRs or where such databases do not exist, the case-population design might give an approximation of the absolute and relative risk when both events and exposures are rare. This is limited by the ecological nature of the reference data that restricts the ability to control for confounding.