Response to the Letter to the Editor Regarding “Fusion Construct Length Is Associated with Increased Risk of Delayed Reoperation Following Cervical and Lumbar Fusion”

We thank the authors for their careful reading of our study and welcome the opportunity to respond. Their comments touch on genuine methodological considerations, which we address in turn below.

Competing risk is a legitimate concern in any survival analysis, and we value the authors highlighting it. In our study, however, the competing risk of mortality is precluded by our cohort construction. As the mechanics of longitudinal follow-up in PearlDiver are rarely detailed in published literature, where published claims-based studies commonly report a “minimum follow-up” without specifying whether that reflects continuous database activity, an analytic observation window, or both, it is worth clarifying how our cohort design handles censoring. Longitudinal follow-up is established through the ACTIVE command, which sets a floor for continuous database activity, 2-, 5-, and 10-years in the present study, while the analytical time horizon is defined separately by hard-coded logic or by the time-dependent analyses themselves. Critically, ACTIVE functions as an inclusion criterion, selecting only patients who meet this minimum tracking requirement. We used the command to construct cohorts such that every patient was continuously observable for the full corresponding time horizon. Consequently, no censoring was required, and mortality could not act as a competing risk within the observation window. The 1-year delayed-entry protocol performs as intended, excluding any reoperation occurring before that threshold. Although, this design may introduce a generalizability constraint, since patients who remain continuously active may differ systematically from those who lose coverage or transition to an untracked payer. For transparency, we reported full demographics in Table 1, allowing readers to compare the cohorts across time horizons and assess the influence of this selection criterion on baseline characteristics. Within observable characteristics, the effect appears modest: age, sex, region, and payer distributions remained largely similar, though the 10-year cohort carried a lower ECI and comorbidity prevalence, consistent with a somewhat healthier population.

We agree that the specification of the Cox proportional hazards models within PearlDiver warrants further explanation. The platform supports user-defined covariates, with patient membership determined by coding logic. When such a variable is entered into the model, patients are classified by “True” membership. However, the comparison is made against the remaining eligible pool rather than against a specified reference. This accounts for the difficulty in directly interpreting the level-specific estimates. We acknowledge that the choice of reference influences the absolute magnitude of the level-specific hazard ratios, and this is a true limitation of Cox model survival analyses within PearlDiver. We wholly agree that a propensity score-matched study designed solely to isolate this effect estimate would provide much-needed clarity on the true magnitude of increasing construct levels in reference to the single level. The goal of the present study was to explore all risk factors rather than to reduce their influence through rigorous matching, and we encourage future research to address this question directly.

The authors aptly note that an effect estimate whose confidence interval excludes zero paired with a nonsignificant p-value for a single outcome appears inconsistent. The discrepancy arises because the two statistics reported in Table 9 estimate different quantities. Postoperative reimbursement was reported as mean and standard deviation, so a standardized mean difference (SMD) was calculated to convey the magnitude of the between-group difference. However, the data was markedly right skewed at every time horizon, with standard deviations exceeding their corresponding means, a distributional pattern characteristic of healthcare resource use. ¹ Between-group comparisons were therefore assessed using the Wilcoxon rank-sum test, which evaluates differences across the full distribution. ² The SMD and its interval characterize the precision with which the difference in means is estimated, whereas the rank-sum test evaluates whether a randomly selected patient from one cohort incurs higher costs than one from the other. Divergence between the two is expected rather than contradictory under the observed distributional conditions. As these unadjusted comparisons were exploratory between cervical and lumbar cohorts, they warrant cautious interpretation in any case. Although the methods section does not explicitly link SMD with the p-value, we acknowledge that presenting them together in Table 9 may reasonably suggest that the p-value corresponds to the effect estimate, as it does in the other bivariate analyses in this study. We appreciate the authors drawing attention to this ambiguity.

We are grateful to the authors for the time taken to raise these points and for the opportunity to engage in this discussion. Claims-based databases offer a valuable means of examining associations within a large national claims cohort, while carrying inherent limitations related to longitudinal eligibility, coding, and model specification. We hope that future work builds on the risk factors identified in the present study, including construct length, to further characterize differences in postoperative risk.

ORCID iDs

Evan R. Simpson https://orcid.org/0009-0004-6507-5326

Zachary T. Mills https://orcid.org/0009-0004-0518-6729

Consent for Publication

All authors provide informed consent for publication.