RE: Outcomes of Root Canal Treatment in Patients With Autoimmune Disease: A Retrospective Case–Control Study

Dear Editor,

This letter is in response to the article by Lee et al. (2026), entitled ‘Outcomes of Root Canal Treatment in Patients With Autoimmune Disease: A Retrospective Case–Control Study’, published in the International Endodontic Journal. After careful reading of the methodology used in this study, there seems to be a potential misclassification of the study design. This is an issue that has been identified and discussed in other disciplines, yet still occurs. (LeBrun et al. 2020; Esene et al. 2018) The purpose of this letter is to discuss and raise awareness of this issue to minimize it occurring in future research. Further, we have used this as an opportunity to highlight issues with communicating statistical analyses and results within this article too.

The study by Lee et al. tests the hypothesis that autoimmune disease is a determinant of root canal treatment outcome, the exposure variable is the presence of autoimmune disease at baseline, and the outcome variable is the nonsurgical root canal treatment outcome. Although the authors describe the study as a retrospective case–control design, the methods indicate a direction of inquiry from exposure to outcome, which would be better classified as a cohort study. If this were a case–control study, the direction of inquiry would be from outcome to exposure. Cases and controls would be selected based on outcome status (e.g., success or failure of nonsurgical root canal treatment), and the investigators would then work backwards to identify prior exposure (e.g., presence or absence of autoimmune disease), for comparison between groups. In contrast, the present study has grouped cases and controls according to exposure status (autoimmune disease vs. non‐autoimmune disease) and subsequently evaluated the outcome of nonsurgical root canal treatment. This design is characteristic of a cohort study, and the study groups should be defined as exposed and unexposed groups rather than case and control groups.

Misclassification and incorrect labeling of observational study designs are recognized methodological problems, and this is not solely an issue of semantics; mislabeling leads to incorrect analysis plans and misinterpretation of findings (Pérez‐Guerrero et al. 2024; Mayo and Goldberg 2009). For instance, cohort studies commonly use a log‐binomial regression model to estimate the risk ratio. In contrast, in case–control studies, the risk ratio cannot be calculated, and logistic regression models are typically used to estimate odds ratios. The odds ratio is less intuitive than the risk ratio and overestimates the magnitude of effect when the outcome frequency is greater than 10%, as in this study (Farajollahi et al. 2026). Thus, if the study is classified as a cohort study, log‐binomial regression should be used instead of logistic regression to estimate a more appropriate measure of effect size. This is one of the reasons why correct identification of study design requires careful attention.

Classifying the study as a case–control design rather than a cohort study appears to have led to additional suboptimal methodological choices, particularly in the selection of the control group. By treating the analysis as case–control, the authors relied on a restricted matched control group. Conversely, a cohort framework would have permitted the use of the entire non‐exposed (non–autoimmune disease) population to act as a control. Applying propensity score (PS) methods to weight the full comparison group would have increased the effective sample size and likely improved the precision of the estimated effects. These issues stem directly from the misidentification of the study design as case–control, rather than cohort.

The description of the statistical analysis in this study can be improved as it lacks precision in details that would support transparency in reporting and reproducibility of the findings. The issues include:

• The derivation of the PS used for matching is briefly described, with no clear specification of the model structure used in their calculations. The statistics presented in table 2 suggest that balance across covariates was close but incomplete.

• The models used to assess the relationship between predictors and outcomes are imprecisely specified. A generalized estimating equation (GEE) approach is mentioned, and chi‐square statistics are reported but there is an absence of information regarding the assumed distribution family and link function. This precludes evaluation of whether the model was appropriate for the outcome data. The subsequent sentence states that multivariable logistic regression is used but it is not explicitly stated that this model was used in previous analyses.

• The repeated measures and correlation structures used for the GEE are not specified. It is left for the reader to assume the method of analysis was correctly applied when analysis includes clustering with multiple teeth per participant as the primary analysis unit. Failure to explicitly account for clustering leads to underestimated standard errors and inflated type I error rates.

• The terms ‘multivariable’ and ‘multivariate’ have been used interchangeably in the abstract and main text. However, these refer to two different types of analyses that are frequently misused. Multivariable analysis involves one outcome variable and multiple exposure variables, whereas multivariate analysis involves the simultaneous analysis of multiple outcomes and multiple exposure variables (Ebrahimi Kalan et al. 2021).

In addition, the reporting of results in table 5 is incomplete, as beta estimates and odds ratios are presented without their corresponding 95% confidence intervals. These are instead confined to the text only. Confidence intervals are essential for interpreting the precision and clinical relevance of effect estimates and should be presented alongside point estimates (Farajollahi et al. 2026). Finally, the structure of table 5 suggests an iterative model‐building process. However, there is no description provided regarding the criteria used for variable selection or model refinement and it was left for the readers to assume that it was fit using a step‐wise model building method. Without this information, readers cannot assess the robustness of the final model, the risk of overfitting or the potential for data‐driven conclusions. Collectively, these omissions limit the ability to critically appraise the validity of the analyses and weaken confidence in the reported results.

Misclassification of the study design and insufficient reporting of analytical details limit the interpretability and robustness of the findings from Lee et al. (2026). It is unclear whether re‐analysis using a cohort framework would change results; however, without this, readers are left wondering. Clarifying and improving reporting the statistical analysis would strengthen the conclusions drawn and improve the contribution of this work to the endodontic literature.

Author Contributions

Mehran Farajollahi: conceptualization (lead), writing – original draft (lead), writing – review and editing (equal). Christopher T. Sexton: writing – original draft (supporting), writing – review and editing (equal), supervision (lead).

Conflicts of Interest

The authors declare no conflicts of interest.

Data Availability Statement

Data sharing not applicable to this article as no datasets were generated or analysed during the current study.