Counting Every Way a Rheumatoid Arthritis Drug Fails: A Competing-Risk Cohort Study of Biologic Choice

Roughly 30–40% of people with rheumatoid arthritis (RA) do not respond adequately to their first biologic drug, and only about half achieve a lasting response (Salehi et al.). A drug can fail in two ways. It may not control the joint inflammation, or it may control it but cause harm the patient cannot tolerate, such as serious infection, liver injury, or the bone and heart damage that comes with steroids taken alongside it. Most real-world comparisons of RA drugs track only the first kind of failure. They treat patients who stop a drug because of side effects as if they had simply left the study. This is unlikely to be harmless bookkeeping, because the patients most likely to quit for toxicity are the older, sicker, more heavily co-medicated ones whose outcomes would also have differed.

We propose a retrospective cohort study that records every way a drug can fail. For RA patients starting a biologic or targeted synthetic drug, we follow each person from the start date to whichever comes first: lasting disease control while still on the drug, stopping for lack of effect, stopping for an adverse event, or death. We then estimate, with confounding adjustment, how the probabilities of these outcomes differ across the main drug classes: tumor necrosis factor inhibitors (TNFi), the interleukin-6 receptor blocker tocilizumab, abatacept, and Janus kinase (JAK) inhibitors. The question is whether drug rankings and subgroup recommendations built from efficacy-only analyses still hold once toxicity-driven stopping counts as failure.

Core Claim

Our hypothesis is that efficacy-only cohort analyses of RA drug classes are biased by informative censoring. Patients who stop for toxicity are removed from the analysis as though their outcome were unknown, when in fact they have failed. If this hypothesis is right, it should show up as measurable shifts in class rankings and in reported subgroup effects. We formalize the outcome as a set of cumulative incidence curves. For drug class $a$, $F_k^a(t)$ is the adjusted probability that a patient starting $a$ has reached state $k$ by time $t$. Here $k$ is one of four states: sustained control on drug, stopped for inefficacy, stopped for an adverse event, or died. By construction,

$$\sum_k F_k^a(t) + S^a(t) = 1,$$

where $S^a(t)$ is the probability of still being on drug and not yet classifiable. The quantity clinicians actually need is the contrast in $F_{\text{control}}$ between classes, read alongside the contrast in $F_{\text{AE}}$ (stopping for an adverse event). Efficacy-only methods cannot provide either contrast honestly.

A second, applied payoff connects to the preclinical literature on safer alternatives. Botanical and targeted compounds are repeatedly presented as avoiding the "toxicity ceiling" of conventional drugs. Examples include NLRP3-inflammasome suppression by the Shi Wei Ru Xiang pill as an alternative to colchicine (Wang et al.), NF-κB down-regulation by Chrysanthemum zawadskii extract in mouse arthritis (Kim et al.), and synovial-fibroblast suppression by the Juanbi Qianggu formula (JBQG). Yet nobody has stated how large that ceiling is in real patients. These papers motivate the question but supply no human data. The adjusted $F_{\text{AE}}^a(t)$ curves would give any future adjunct or alternative a concrete real-world benchmark to beat.

Research Program

The design is a target-trial emulation. We specify the randomized trial we would like to run and then mimic its eligibility rules, start time, and comparison groups using historical records. The study uses a new-user, active-comparator design. Eligible patients have RA, have previously used a conventional DMARD (disease-modifying antirheumatic drug, such as methotrexate), and are starting their first biologic or targeted synthetic drug. Time zero is the start date. Comparators are the other drug classes, never untreated patients.

The primary cohort is the Swiss Clinical Quality Management in Rheumatic Diseases (SCQM) registry. It is the only resource in our file that records both repeated disease activity scores and the stated reason for stopping a drug (inefficacy versus adverse event). Siegel et al. used it with $n=3{,}516$ first-biologic starters. Sustained control is defined as low disease activity on DAS28-ESR, a 28-joint disease activity score using the erythrocyte sedimentation rate. Specifically, DAS28-ESR must stay below 3.2 at two consecutive visits while the patient remains on drug, with remission (DAS28-ESR below 2.6) as a secondary threshold. This deliberately replaces the coarse "20% reduction" proxy that Siegel et al. used.

Confounding by indication is handled with multinomial propensity scores and overlap weights over baseline demographics, serostatus, disease duration, DAS28-ESR, HAQ (a functional disability questionnaire), prior conventional DMARD count, baseline prednisone dose, and comorbidities. Propensity scores are each patient's estimated probability of receiving each drug class given these characteristics. Overlap weights emphasize patients who could plausibly have received any class. Cumulative incidences are estimated with a doubly robust Aalen–Johansen-type estimator, which remains consistent if either the treatment model or the outcome model is correct. Steroid tapering and added conventional drugs after time zero are time-varying, so a per-protocol secondary analysis uses inverse-probability-of-censoring weights for these deviations.

Registry visits are irregular, which means sustained control can only be observed at visits. We therefore define states on a visit grid and test sensitivity to visit frequency, including modeling visit intensity as a function of prior disease activity.

Rare toxicities such as serious infection, herpes zoster, venous thromboembolism, major cardiovascular events, and fracture are too infrequent for SCQM alone. For these we run a companion safety analysis on OMOP-standardized claims and EHR databases of the kind used by Lane et al., such as CPRD, Optum EHR, and MarketScan. That study ran a ten-database, 1.2-million-patient comparison of hydroxychloroquine versus sulfasalazine. We reuse its method: active-comparator propensity matching, per-database Cox models, random-effects pooling, and empirical calibration against negative-control outcomes. Negative controls are outcomes believed unaffected by either drug, so any apparent effect on them measures residual bias. We extend that method from a single psychiatric endpoint to a panel of multi-organ toxicities across biologic classes. Finally, a transportability step reweights the OMOP cohorts to SCQM's covariate distribution. This lets us check whether the registry's "stopped for adverse event" rates are consistent with coded toxicity rates in the larger network.

Baselines

The naive reference point is a crude comparison: Kaplan–Meier "drug survival" curves by class, with no adjustment and with adverse-event stops censored. This is still how many registry reports present drug retention. Any adjusted method that cannot move these curves where confounding is plausible is not doing work.

The strongest existing efficacy-side method is the approach of Siegel et al., Cox regression for discontinuation due to non-response with adverse-event stops treated as censored, stratified by patient subgroups. Their reported numbers are a hazard ratio of 5.46 for tocilizumab response in patients with two or more prior conventional DMARDs plus baseline prednisone, 8.44 in men, and 3.64 in patients with lower disease burden. For golimumab non-response they report a hazard ratio of 2.36 in seronegative women without prednisone and 5.27 in seropositive women with high burden and long disease duration. We rerun this on the identical SCQM extract with the same covariates and follow-up, defining subgroups by their stated clinical indicators rather than by re-deriving the clusters, which required manual visual inspection. Our method "beats" it in a specific sense: if adding adverse-event stopping as a competing failure shifts any of these subgroup contrasts outside the efficacy-only confidence interval, the efficacy-only figures were not estimating what clinicians assume they estimate.

The strongest existing safety-side method is the calibrated network design of Lane et al.. For hydroxychloroquine versus sulfasalazine, that study reports a 30-day depression hazard ratio of 0.96 (95% CI 0.79–1.16). For the biologic-class toxicity contrasts we target, no reported result was found on Lacuna. We apply their pipeline unchanged, per outcome, as the baseline. Our contribution is not a better hazard ratio per outcome but placing those hazards in the same competing-risk frame as efficacy.

For prediction rather than causal contrast, the reference is Salehi et al.. They report XGBoost AUC-ROC of 0.91 for 6-month response and AdaBoost AUC-ROC of 0.84 for 12-month sustained response in a single-center cohort of 154 patients. We refit both models with nested cross-validation on SCQM, for the same endpoints and for our four-state outcome. This tests whether those AUCs survive a larger multicenter cohort and whether adding toxicity as a failure mode makes "response" harder to predict.

The key ablation removes the one ingredient we claim matters. We run the full doubly robust, weighted analysis twice, once with adverse-event stops as a competing failure and once with them censored, keeping everything else fixed. The size of that difference is the paper's main estimate.

Why not just…?

Why not just run the Lane et al. pipeline separately for each efficacy and safety outcome? This is the most serious alternative, and it may largely suffice. Separate per-outcome hazard ratios are well calibrated, but they answer "how fast does event X happen among those still at risk." They do not answer "what fraction of starters end up controlled and tolerating the drug." When toxicity and inefficacy remove different kinds of patients, these two questions can give different rankings. The ablation above settles it. If competing-risk and per-outcome rankings agree in every subgroup, we will report that efficacy-only practice is robust in this setting, which is itself a useful negative finding. The negative-control machinery is reused, not replaced.

Why not just run a randomized trial? Head-to-head biologic trials typically run 12–24 weeks with restrictive eligibility. They are too short and too small to observe the delayed fractures, cardiovascular events, and infections that drive real-world stopping in multimorbid patients, and they cannot cheaply cover four drug classes and many subgroups. Our emulation is meant to tell trialists which contrasts and subgroups are worth randomizing.

Why not just fit a better predictive model or deep clustering? Predictors like those of Salehi et al. estimate who responds to biologics in general, not what would happen to the same patient under a different class. Clustering as in Siegel et al. still needs a causal contrast within each cluster, and its boundaries were set by hand. We include both as baselines rather than ignoring them.

Why not use a deep causal survival model such as DynST? Chatha et al. combine a transformer over longitudinal EHR features with doubly robust adjustment. On semi-synthetic MIMIC-III intensive-care data, they report a survival MAE of 11.19 versus 11.42 for a static transformer and 16.04 for an oracle Cox model. That gain is small, it was measured in hourly ICU data rather than sparse outpatient visits, and the bias we target comes from the outcome definition, not the model's flexibility. We therefore test it in the simulation below and adopt it only if it clearly reduces bias there. The same reasoning applies to the latent-confounder approach of the Medical Deconfounder, which assumes static exposures. We use it only as a sensitivity analysis on baseline co-medication patterns.

Decisive Experiments

The first check is a plasmode simulation, meaning simulated outcomes generated on top of real patient covariates. Using real SCQM covariates and treatment assignments, we simulate outcome states with known class effects, letting toxicity-driven stopping depend on baseline severity and steroid dose as clinical practice suggests. We then measure bias and confidence-interval coverage for the naive estimate, the efficacy-only Cox model, separate per-outcome hazards, our competing-risk doubly robust estimator, and a DynST-style variant. The proposal fails if efficacy-only bias is negligible under realistic informative stopping.

The second check is the real-data ablation. It compares class rankings and the five Siegel subgroup contrasts with and without competing-risk treatment of adverse-event stops. The third is negative-control calibration in both SCQM and OMOP. If the empirical null from negative controls is wide, we report calibrated intervals and temper the claims accordingly.

The fourth check is cross-source consistency. Transported OMOP toxicity rates should bracket SCQM's adverse-event stopping rates. If they disagree, that indicates under-recording of toxicity in one source, which we would report rather than smooth over.

The deliverable is a set of adjusted four-state outcome curves per drug class and subgroup. Together they give a real-world estimate of the toxicity ceiling that any safer alternative therapy would have to undercut.