Improving rheumatoid arthritis comparative effectiveness research through causal inference principles: systematic review using a target trial emulation framework

Abstract

Objectives.

Target trial emulation is an intuitive design framework that encourages investigators to formulate their comparative effectiveness research (CER) question as a hypothetical randomised controlled trial (RCT). Our aim was to systematically review CER studies in RA to provide examples of design limitations that could be avoided using target trial emulation, and how these limitations might introduce bias.

Methods.

We searched for head-to-head CER studies of biologic DMARDs in RA. Study designs were reviewed for seven components of the target trial emulation framework: eligibility criteria, treatment strategies, assignment procedures, follow-up period, outcome, causal contrasts of interest (i.e., intention-to-treat or per-protocol effect) and analysis plan. Hypothetical trials corresponding to the reported methods were assessed to identify design limitations that would have been avoided with an explicit target trial protocol. Analysis of the primary effectiveness outcome was chosen where multiple analyses were performed.

Results.

We found 31 CER studies, of which 29 (94%) had at least one design limitation belonging to the seven components. The most common limitations related to: 1) eligibility criteria: 19/31 (61%) studies used post-baseline information to define baseline eligibility; 2) causal contrasts: 25 (81%) did not define whether intention-to-treat or per-protocol effects were estimated; and 3) assignment procedures: 13 (42%) studies did not account for confounding by indication or relied solely on statistical confounder selection.

Conclusions.

Design limitations were found in 94% of observational CER studies in RA. Target trial emulation is a structured approach for designing observational CER studies that helps to avoid potential sources of bias.

Introduction

There are a growing number of pharmacological treatment options in rheumatology, particularly high-cost biologic and targeted synthetic disease modifying anti-rheumatic drugs (bDMARDs and tsDMARDs). This enlarging armamentarium begs the question of how to choose the optimal treatment for a given condition. Head-to-head randomised controlled trials (RCTs) of these new and emerging therapies – the preferred evidence – are scarce and provide only limited guidance; for example, few have directly compared treatment options for rheumatoid arthritis (RA) patients who have failed one or more bDMARDs. When RCTs are not feasible, timely, or ethical, observational data can help fill the need for comparative effectiveness information ^1–3.

Observational comparative effectiveness research (CER) studies are common in rheumatology, as are their critics. The target of much criticism lies in the sheer number of methodological approaches available to the analyst ⁴, and the profound effect that nuanced differences in methods can have on results ^5,6. Large sample sizes in these studies may instil false confidence in the presence of critical design flaws. Improvement and standardisation of methodology guided by causal inference principles are paramount and increasingly demanded by many clinical journals ⁷. One barrier, however, is that detailed theory based on “potential outcomes” ⁸ can seem complex and unfamiliar.

A more intuitive approach is to ask: “How would I answer my CER question as an RCT?” according to the recently popularized “target trial emulation” framework of observational study design and analysis ³. This way of thinking is rooted in the principles of causal inference, which were first conceived in the context of randomized experiments ⁹ and extended to observational studies ^2,10,11. Principled re-analyses of existing observational studies using the target trial emulation framework have repeatedly shown to reduce bias and better align results with actual RCTs ^6,12–16.

Through a systematic review of observational CER studies in RA, we provide examples of design limitations that might have been avoided by using target trial emulation, and how these limitations might introduce bias. Since the practice of explicitly writing down the target trial protocol is relatively new ³, we did not expect the reviewed study designs to incorporate its terminology; rather, we retrospectively imposed the framework components as a structured way to appraise them.

Methods

Target trial emulation framework

At the heart of the target trial emulation framework are two protocols –”target trial protocol” and “emulation protocol”– for each observational CER study (Figure 1). When prospectively designing an observational CER study, researchers first consider how the question can be answered and formulated as a hypothetical RCT — the “target trial” ³. Systematically specifying this protocol helps ensure that the question is clinically meaningful for decision making (e.g., “among eligible patients, which treatment strategy maximizes benefit?” rather than simply “is exposure X associated with outcome Y?”)^17,18. The “emulation protocol” describes how available observational data might be used to obtain the best approximation of the “target trial protocol”. The protocol is then reformulated when data limitations and feasibility of the ideal emulation are realised (Figure 1) ¹⁰. This framework helps to avoid common methodologic pitfalls^3,19 and better align results with RCTs.

Figure 1.

The target trial protocol is used to guide observational comparative effectiveness research design. This idealized protocol may need to be reformulated once limitations of the data are realised. Divergence of the implemented observational study (emulation) from the target trial protocol should be addressed by sensitivity analyses or transparent reporting of limitations.

The framework can also be applied retrospectively for appraising existing studies in a structured process ³. The description of an observational CER study can be seen as the emulation protocol for the inferred target trial. After inferring the corresponding target trial protocol, it is possible to assess the clinical question ^17,18 as well as subtle design limitations that fail to emulate a sound target trial ¹⁹. This retrospective application is our approach in this review.

Systematic literature review

We searched EMBASE, Medline and PubMed in August 2019. Search terms are shown in online supplementary materials. We only included head-to-head effectiveness comparisons to demonstrate the utility of target trial emulation beyond existing good design practice (Supplementary Table S1) ^4,20,21. We restricted to comparisons of different classes of bDMARDs, where RCTs are scarce but evidence is needed to guide clinical practice. Studies that did not report effectiveness (i.e., only reported drug retention or adverse/comorbidity events) were excluded. Independent reviewers (SSZ, HL) assessed study eligibility and performed data extraction (Table 1 and Supplementary Table S2); discrepancies were resolved through discussion moderated by a third reviewer (KY). Where multiple analyses were presented in one study, analysis for the primary effectiveness outcome was chosen. We appraised each study’s design against each of the target trial emulation components below ³; the specific questions we asked of each study’s design (i.e., data extraction items) are listed in Table 1 (left column).

Table 1.

Items in the pre-specified data extraction form and a summary of findings from 31 studies.

	Data extraction questions (See Methods for rationale)	Summary of findings from 31 studies*
1. Eligibility criteria	What were the criteria? (e.g., classification criteria RA with no prior exposure to bDMARDs)	All studies specified basic eligibility criteria such as RA definition, level of disease activity and number of prior bDMARDs.
	Was post-baseline information used to define eligibility? (e.g., requiring ≥1 follow-up)	19/31 (61%) studies explicitly required post-baseline information for eligibility 29–47.
	How many bDMARDs had been used before? (e.g., bDMARD naïve, ≥1 prior TNFi)	All studies described the number of prior bDMARDs. 5/31 (16%) studies combined response from both bDMARD-experienced and naïve patients 40,44,48–50.
2.Treatment strategies	What were the bDMARDs under comparison?	Drug name, dose and frequency were generally clearly defined, except when different TNFi were combined as one group.
	What were the treatment strategies? (e.g., discontinuation due to remission or switch to biosimilar are permitted in the protocol)	One study clearly defined treatment strategies 51.
3.Assignment procedures	How did the study use statistics to emulate random assignment? Specifically, how were confounding factors selected?	13/31 (42%) studies used only pre-defined confounders 31–34,36–38,41,44,46,52–54. 5/31 (16%) studies used only statistical (e.g., p-value-based) variable selection 29,30,43,45,47. 9/31 (29%) made no adjustments for confounding beyond active-comparator design 39,40,42,47–50,55,56.
4.Follow-up period	What was the specified duration of study? For studies using existing data from registries, duration of the implied trial was used.	Studies using binary response outcomes clearly defined follow-up times in all except one study 41. 6 studies did not specify an end to follow-up at all 30–32,40,41,54.
5.Outcome	What was the primary effectiveness outcome measure and timeframe/point?	Outcomes were clearly described, but time occasionally not (see above).
	Was sample size or statistical power discussed at the design stage?	4/31 (13%) studies included sample size considerations 29,31,43,52.
6.Causal contrast of interest	Was a causal contrast of interest declared prior to analysis?	6/31 (19%) studies clearly defined causal contrast 31,47,49–51,53.
	What was the declared or inferred causal contrast?	20/31 (97%) studies examined some version of the ITT effect 29,31,33–37,39,41,43,44,46–48,51,53,54,57–59; analyses were compatible with traditional ITT effect definition in only 1 study 53. 12/31 (42%) studies include per-protocol analysis 30–32,38,40,42,45,49–52,55 but did not apply any post-baseline adjustments.
7.Analysis plan	What statistical model was used? (e.g., linear regression)	18/31 (42%) studies used regression-based methods. 8/31 used pairwise comparisons and 3/31 did not perform statistical comparison.
	How were missing data handled? (e.g., complete-case analysis, imputation)	17/31 (55%) studies used complete-case analysis 29–33,39,41,43,44,47–49,52,55,56,58,59. 3/31 used multiple imputation for missing outcome data51,52,57. 9/31 use single imputation34–38,45,46,53,54. Reasons for discontinuation were rarely differentiated in analyses

^*Components of the target trial emulation framework are discussed in detail in references 3 and 6. See Results for details; information extracted from individual studies are shown in online Supplementary Table S2.

1. Eligibility criteria.

All RCTs are expected to have clear, predefined eligibility criteria before the study begins. Those with contraindications to any of the treatment strategies must be excluded. Obviously, RCT eligibility criteria can only consist of baseline information that are available to investigators at the time of prospective enrolment. To emulate such a target trial, observational cohorts first need to be defined using information up to the baseline (often called “time zero”), but not beyond ³. For example, some observational studies require at least one follow-up in the eligibility criteria. This practice does not have an RCT equivalent, since trial investigators cannot see into the future at the time of each patient’s enrolment. Cheating the baseline criteria via such an oracle can bias results in either direction ²².

Including key confounders in the emulation eligibility criteria may help comparability. One example is the number/type of prior bDMARD failure; prior bDMARD failure is an important predictor of response. This is intuitive when conceptualised as equivalent RCTs: a trial comparing bDMARD naïve patients, or a trial comparing switching of therapy after one or more TNFi failures. We examined each study’s eligibility criteria for use of post-baseline information and specification of the prior bDMARD treatment history (Table 1).

2. Treatment strategies.

An RCT protocol specifies detailed treatment strategies beyond the drug name. The protocol also defines criteria for discontinuation or modification, and relevant concomitant care that are allowed or prohibited during the follow up ²³. Each major treatment change should be defined as complying with or violating the protocol. For example, change of concomitant csDMARDs or discontinuation of bDMARD due to remission may be protocol-compliant, whereas switch to another bDMARD due to insufficient response may be considered a protocol violation. How treatment strategies are defined will have implications for the definition and analysis of the per-protocol effect (components 6 and 7). Observational CER studies also have to specify treatment strategies. Not all datasets have enough details to define granular treatment strategies, which may require the emulated target trial to be simplified (Figure 1). We reviewed how treatment changes were defined as part of the treatment strategy.

3. Assignment procedures.

In the simplest RCT design, participants have equal chance of being assigned to each treatment strategy, and each treatment group will have comparable distribution of prognostic factors. To emulate random treatment assignment in observational CER, all theoretical confounding factors - measured and unmeasured - need to be adjusted for. Inability to completely account for confounding is the commonest criticism for observational studies. While this may be the case, there are many ways to improve emulation of random assignment. Two considerations are the use of active-comparators ²⁰ (which should be present by default in head-to-head comparisons) and methods for selecting confounders ²⁴. Confounding factors should not be selected solely based on their statistical association with the exposure or outcome. Selection should instead be based on subject knowledge and/or literature review, preferably supported by directed acyclic graphs (DAGs) that make assumptions transparent ²⁴. For the review, we focused on how confounding factors were selected.

4. Follow-up period.

RCTs have a well-defined start, schedule and end of follow-up. In rheumatology trials, efficacy typically focus either on percentage of participants achieving a response definition at a certain time-point or multiple repeated assessments over the study period. Each RCT participant is consented for a schedule of follow-ups and a finite study period (e.g., 12 months after treatment initiation). By contrast, observational data often come from ad hoc clinic visits, where frequency may be associated with patient and disease characteristics. The data to be used in an observational analysis should ideally reflect the same (or similar) data that would have been collected in the target trial ²⁵. This reduces issues from differential health utilization and provides greater structure for missing data assessment. We assessed whether duration to end of follow-up was defined.

5. Outcome.

RCT outcomes typically include a response definition at a certain time point, e.g., DAS28<2.6 at week 12. In observational CER, an appropriate outcome definition also needs to be accompanied by assessment time(s), which is why follow-up needs to be clearly prespecified. A common practice for binary response outcomes is to include assessments within a certain window (e.g., 12 ±3 months), but this is less commonly considered for repeated continuous outcomes (e.g., use all available follow-up DAS28 scores).

The choice of RCT outcome is often linked to power (sample size) calculations. This is not a component in the target trial emulation framework ³, but an underpowered observational study can only emulate an underpowered RCT at best. In the majority of observational CER studies, sample size is not a decision. Investigators should estimate whether there is sufficient power to pursue their analysis at the design stage. Underpowered endeavours should be avoided or at least highlighted as a major limitation. Note that post hoc power calculations, whether in trials or emulations, are not informative ^26,27. We reviewed whether outcomes were clearly defined and whether statistical power limitations were discussed.

6. Causal contrast of interest.

Researchers should clearly define the answer they want – the intention-to-treat (ITT) or per-protocol effect – before thinking about the data or analysis ²⁸, in observational CER studies as is the standard for RCTs. The two estimands require different analyses, have different interpretations and often have different effect sizes. In RCTs, ITT analyses estimate the effect of being assigned to treatment strategies, regardless of what happens thereafter (even if treatment is not initiated). The observational analogue of the ITT effect is the effect of initiating the treatment strategies; i.e., ITT analysis will include outcomes from patients who remained on and those who discontinued the drug (or deviated from the protocol in any other manner). The per-protocol effect is the effect of the treatment strategy when fully adhered to, hence the importance of clearly defining it. Discontinuing treatment (for whatever reason) may be the only specified “protocol deviation” in observational CER studies, in which case per-protocol analysis will include only the “on-treatment” population. We assessed whether the authors defined their causal contrast of interest and what they were.

7. Analysis plan.

Analyses for the ITT effect in RCTs do not require confounding-adjustment and is the direct comparison of the average outcomes of treatment arms. However, in the presence of differential loss-to-follow-up, missing data handling that preserves the original randomized cohort are required for valid ITT analysis (e.g., by imputing non-response). By contrast, analysis for the per-protocol effect occurs in a subset of data that artificially censor individuals at the time they deviated from the treatment strategies. Such non-random censoring likely introduces selection bias. Advanced statistical methods using post-baseline time-varying covariates are required to adjust for this bias ³. We reviewed analysis plans together with the declared or implied causal contrast as above.

The analysis plan in the emulation protocol should look identical to the target trial protocol except for the need to adjust for baseline confounding. Treatment strategy, causal contrast and analysis plan are dependent upon each other and were reviewed together. Where causal contrasts were not declared, we assessed how censoring was defined in each study (i.e., treatment strategies) to infer the authors’ implied causal contrast. The chosen statistical method affects how missing data and censoring are handled; we therefore reviewed the statistical model and missing data handling in this section.

Results

A total of 31 studies met our inclusion criteria. The selection flowchart is shown in Supplementary Figure S1. 21 studies compared bDMARDs from two classes ^{29–40,43,45,47,52–54,56,57,59} and 10 compared three or more classes ^{41,42,44,46,48–51,55,58}; there were no studies of tsDMARDs. Information extracted from each study are detailed in supplementary Table S2. Only one study explicitly emulated a target trial ⁵³.

1. Eligibility criteria.

19 out of 31 (61%) studies explicitly included post-baseline information in their eligibility criteria by requiring at least one follow-up ^29–45 and/or a minimal duration of follow-up ^46,47,59. The proportions of participants excluded without follow-up were typically large (up to 69% ³⁴), but frequently unreported. An additional seven studies ^{48–50,52,55,56,58} implicitly made these exclusions (up to 82% ³³) by using complete-case analyses.

10 studies specified an exact number of prior bDMARDs, while 21 studies included varying numbers of prior bDMARD failure. 12 studies combined bDMARD experienced patients (i.e., ≥1 prior bDMARD failures) or stratified analyses to that effect ^{30–37,44,46,54,58}. Eligibility criteria of nine studies included both bDMARD naïve and experienced patients, among which five did not stratify to separate treatment effect for these two groups ^{40,44,48–50}.

2. Treatment strategies.

Treatments under comparison were well defined, but not treatment strategies. Only one study ⁵¹ defined whether treatment changes were protocol compliant (e.g., biosimilar switch and discontinuation due to remission were permitted). Studies comparing bDMARD monotherapy ^37,49,50,54 were unclear whether initiation of csDMARD (although rare in clinical practice) would be artificially censored. Due to limited descriptions of treatment strategies, we instead examined what investigators artificially censored in the analysis to infer what they considered protocol compliant (i.e., whether discontinuation was censored; see Supplementary Table S2). However, what the authors censored was not always clearly described.

3. Assignment procedures.

13 of the 31 (42 %) studies used only pre-defined confounders ^{31–34,36–38,41,44,46,52–54}; none explicitly cited literature review or DAGs. Five (16%) studies used only statistical variable selection ^{29,30,43,45,47}, such as univariate or stepwise P-value-based selection, or change-in-outcome selection. One study included post-baseline variables in the selection process ²⁹. Nine (29%) studies performed no adjustments for confounding ^{39,40,42,47–50,55,56} (one deliberately excluded baseline values of the outcome ³⁰). Active-comparator, new-user design was used in all except one study that included both new and prevalent users ⁵⁰.

4. Follow-up period.

14 of 31 (45 %) studies used binary outcomes with clear assessment time points akin to RCTs, thereby defining their end to follow-up ^{35,41,42,45,46,48,50,51,53–57,59}. 18 (58 %) studies included continuous outcomes (e.g., DAS28 over time), among which six did not specify an end to the study period ^{30–32,40,41,54}. This was typically when linear mixed models were used with all available data. One extreme example used the last available follow-up before therapy switch, which could be any time-point beyond 1 year ⁴¹.

5. Outcome.

Outcomes were clearly defined in all studies. Only four studies (two of which adopted RCT design) explicitly performed sample size calculations ^29,31,43,52. There was typically no discussion about power limitations, even when sample sizes were as small as <50 in each arm ⁵⁸. Four studies reported a joint outcome ^42,50,51,54, i.e., the proportion achieving response and remaining on drug. When this was achieved using LUNDEX (“fraction of starters still in the study multiplied by the fraction responding” ⁶⁰), statistical comparisons and confidence intervals were not provided.

6. Causal contrast of interest.

Only six studies defined their causal contrasts prior to describing analyses ^{31,47,49–51,53}. Inferring from analysis methods, 20 studies included some version of the ITT effect ^{29,31,33–37,39,41,43,44,46–48,51,53,54,57–59}; all except one ⁵³ excluded patients without follow-up (through eligibility criteria or complete-case analysis) which is not compatible with the traditional ITT definition. 12 studies declared or implied per-protocol effects in part of their analysis ^{30–32,38,40,42,45,49–52,55}, but none subsequently adjusted for post-baseline time-varying confounding. Causal contrasts could not be clearly determined in two studies, due to inclusion of prevalent users ⁵⁰ and lack of clarity on whether discontinuation was defined as non-response ⁵⁶.

7. Analysis plan.

Most studies either used (generalised) linear models for outcomes at a fixed time-point ^{35,36,41,43,44,51,53,57,59}, or linear mixed models for repeated continuous outcome measures ^{30–34,37,45,47,54}. One study used generalised estimating equations ⁴⁶. Eight studies used pairwise comparisons (e.g., t-test, chi squared test) or ANCOVA ^{29,39,48,49,52,55,56,58}. Three studies did not perform any statistical comparison, two of which due to the use of LUNDEX ^42,50.

17 out of 31 studies used complete-case analyses ^{29–33,39,41,43,44,47–49,52,55,56,58,59}. Linear mixed models can handle missing (at random) data by default. Only three studies used multiple imputation for missing outcome data ^51,52,57, while nine studies used single imputation (e.g. last observation carried forward, or non-response imputation) to obtain ITT effects ^{34–38,45,46,53,54}. It was often unclear whether outcomes of those who discontinued treatment were included or excluded from analysis. Reasons for discontinuation (e.g., switch to another bDMARD or biosimilar or remission) were rarely differentiated in treatment strategies which impacts definition of causal contrast and its analysis. The analyses of 10 studies artificially censored individuals discontinuing the initial bDMARD (“on-treatment” analysis) ^{31,37,38,40,42,45,49,50,52,55}.

Discussion

We use the target trial emulation framework to identify design limitations in CER studies in RA. There was significant methodologic variation despite restricting to a relatively narrow topic with simple designs. One study described the target trial⁵³ although not to the extent recommended³. 94% had at least one design limitation with the potential to introduce bias; the most common were: 1) including post-baseline information in eligibility criteria, 2) not defining the causal contrasts (i.e., ITT or per-protocol effects), and 3) inadequate emulation of random assignment with unadjusted comparisons and reliance on statistical confounder selection.

Excluding those without future follow-up in eligibility criteria cannot emulate an RCT. Beyond the conceptual conundrum, this practice can bias results in either direction when loss to follow-up differ across treatment arms and are associated with outcomes ²². Many complete case analyses also implicitly exclude those without follow-up. The underlying motive is to deal with missing data. Naïve methods of missing data handling, such as complete case analysis or single imputation, are not recommended for RCTs ^61,62. This is still more relevant for observational studies where the proportions missing are much higher (the potential for bias increases as the proportion of missing data increases). Larger sample sizes seen in observational CER may instil greater confidence in the wrong result. Common alternative approaches include multiple imputation or likelihood-based methods depending on the pattern of missingness. Defining a follow-up duration and desired outcome assessment times can help assess missing data patterns and mechanisms. Note that the proportion of missing data does not dictate the validity of multiple imputation, rather it is the mechanisms of missingness and amount of information held by auxiliary variables (that inform generation of imputations) ⁶³. Investigators might also attempt to reduce missing data by selecting participants with higher likelihood of follow-up without looking at post-baseline data (analogous to pre-randomisation run-in periods of RCTs ⁶⁴). A full discussion on how to handle missing data is beyond the scope of this review. We instead refer readers to reference ⁶² for an introduction and ^61,65 for comprehensive overview. If analysis restricted to those with follow-up is unavoidable, comparison of included and excluded individuals should be clearly presented as a minimum. However, this would render causal contrasts difficult to define.

Choice of causal contrasts relates to a similar underlying missing data issue. ITT is appealing for its (perceived) simplicity in both trials and observational CER: analyse outcomes in all those assigned treatment strategies regardless of what happens thereafter (i.e., adherence or protocol deviations). Unlike trials, observational data often have significant loss to follow-up. Imputing non-response to all missing cases may result in null ITT effect, even if one treatment is superior. ITT analyses also have limitations when studying harms of treatment and in non-inferiority comparisons ⁶⁶. Per-protocol effects have many advantages over ITT, but valid estimation can be challenging. One case-study against per-protocol effects was the survival difference between adherers and non-adherers to placebo in a cardiology trial, which could not be removed with simple statistical adjustment ⁶⁷. Successful adherence adjustment is possible with modern methods that adjust for post-baseline time-varying prognostic factors ⁶⁷. As is recommended for pragmatic trials, observational CER studies should present both ITT and per-protocol effects ⁶⁶ or, as a minimum, declare the causal contrast before analysis. This was rarely done in the studies reviewed, partly because clear definitions were impossible when post-baseline information was used for eligibility criteria and/or because treatment strategies were not described. Further discussion of causal contrasts and related methods can be found in references ^10,19,68.

Another common design issue was the emulation of random assignment in RCTs. Inclusion of prevalent users was uncommon because we reviewed head-to-head (i.e., active-comparator) studies, but this practice and consequent time-dependent biases are common in the rheumatology literature (e.g., immortal time bias resulting from a period of follow-up during which the study outcome cannot occur ⁶⁹). Applying intuition from the target trial protocol can prevent such “self-inflected injuries” ¹⁹. Selecting an active-comparator with similar indications also has several advantages for confounding adjustment ^20,21. Valid comparison requires individuals to have non-zero probability of receiving either treatment (i.e., no absolute contra-indications). Statistical adjustment for confounding also requires sufficient overlap in participant characteristics across treatment groups, which will be greater when treatments have similar indications; this is also true for unmeasured confounding (e.g., frailty) ⁴.

Approaches for choosing confounders varied. Statistical approaches to covariate selection (e.g., based on statistical associations that are widely used in studies of predictors) should generally be avoided for CER ^7,24. Selection should be based more on subject knowledge and/or literature review, preferably supported by directed acyclic graphs (DAGs) that make assumptions transparent ⁷. This helps avoid including variables that can introduce bias when adjusted, such as mediators (causal intermediate variables that are part of the treatment effect) and colliders (variable causally influenced by ≥2 variables that induces spurious associations if adjusted) ⁷. Adjusting for covariates that are not prognostic but strongly associate with treatment assignment (possible when selection is purely based on statistical associations with treatment group) does little to reduce bias but increase variance ⁷⁰. Declaring a priori confounders also improves transparency, which is another criticism of observational studies ⁵. Propensity score methods - although not necessarily superior to traditional multivariable regression - provide an intuitive emulation of randomization since it separates confounding adjustment from outcome analysis. They also help assess utility of the comparison; for example, analyses should be avoided or cautiously approached when propensity score overlap is poor (i.e., violation of the positivity assumption required for valid causal inference) ⁴.

This review was limited to comparisons of effectiveness, but target trial emulation applies equally to safety and other types of time-to-event outcomes (existing target trial emulation examples are typically applications for the latter). Additional design considerations for studies of safety outcomes, such as infections, are discussed in reference ⁷¹. A central concept in the emulation framework - clear definition of time-zero – may seem obvious in the examples reviewed, but the principle is equally relevant for other observational designs such as case-control studies ^72,73. Our restriction in scope left out secondary analyses, which were also fraught with design issues, e.g., comparisons of a bDMARD as first vs second line treatment ^45,57 (try considering if this can be implemented as an RCT). Post hoc adherence-adjusted response using the LUNDEX ⁶⁰ was found in several papers, with the primary aim of accounting for missing outcome data. Assuming non-informative censoring, the LUNDEX estimates the “proportion of patients who not only remain on a particular therapeutic regimen but also fulfil certain response criteria” ⁶⁰. Adherence issues are avoided at the cost of changing the outcome definition. Future work in this area should incorporate more modern approaches to adherence adjustment ⁶⁷, in emulation of more rigorous definitions and handling of missing data in RCT literature ⁶².

In conclusion, target trial emulation builds on existing good design practices to make robust observational designs intuitive. It ensures that clear and clinically relevant questions are asked, incorporates causal inference principles, and has been shown to better align observational results with actual RCTs. Future CER studies should avoid using post-baseline information to define eligibility, clearly define the causal contrast pursued (ideally presenting both ITT and per protocol effects), and consider confounding using prior knowledge (preferably using causal diagrams that make assumptions transparent). This framework is beginning to be adopted in the rheumatology literature ^53,74, but further improvement and standardisation of CER methodology is essential as more drugs become available, often without (timely) head-to-head RCTs to compare their effectiveness.

What is already known about this subject?

• Target trial emulation is an intuitive design approach that encourages researchers to formulate their question as a hypothetical randomised controlled trial (RCT). Using observational data to emulate such a target trial helps avoid common biases and has been shown to better align results with actual RCTs.

What does this study add?

• Most CER studies in rheumatoid arthritis had at least one design limitation, such as using post-baseline information to define eligibility, not specifying whether interest is in intention-to-treat or per-protocol effects, and using statistical selection of confounders. Each of these issues can introduce bias and affect data analysis and interpretation.

How might this impact on clinical practice or future developments?

• The target trial emulation framework unifies and builds upon existing good design practices to make robust observational designs intuitive. Improvement and standardisation of CER methodology is essential in rheumatology as more drugs become available, often without (timely) head-to-head RCTs to compare their effectiveness.

• Future studies should avoid using post-baseline information to define eligibility, clearly define the causal contrast pursued (ideally presenting both ITT and per protocol effects), and consider confounding using prior knowledge (preferably using causal diagrams that make assumptions transparent).

Data availability statement:

All data relevant to the study are included in the article or uploaded as online supplementary information.