Randomized Controlled Trial of Hip Arthroscopy Surgery vs Physical Therapy :

Dear Editor: We read with great interest the recent article published in AJSM by Mansell et al titled ‘‘Arthroscopic Surgery or Physical Therapy for Patients With Femoroacetabular Impingement Syndrome: A Randomized Controlled Trial With 2-Year Follow-up. ’’ This trial is one of several ongoing randomized controlled trials (RCTs) on this welldeserving topic. The authors should be congratulated for performing an RCT of this nature to attempt to answer this important question. However, we have a number of concerns regarding the authors’ methods, results, and conclusions, and the potential for readers to misinterpret the presented results. These major concerns include (1) a high rate of crossover, (2) a significantly underpowered ‘‘as treated’’ analysis, (3) very small improvements in patient-reported outcomes (PRO) after surgery (which is inconsistent with the previous peer-reviewed literature), and (4) inclusion of patients with less than 2 years of follow-up in the primary analysis. RCTs represent the highest level of evidence given their ability to limit the effect of bias. However, RCTs are not immune to the effect of bias. In fact, some RCTs of lesser quality or with less than 80% follow-up are better classified as level 2 evidence according to the Centre for EvidenceBased Medicine (CEBM) guidelines followed by AJSM. One major source of bias in RCTs is patient crossover, which has the potential to obscure the effect of an intervention. While some patient crossover is unavoidable, efforts to minimize crossover in an RCT are important. Intention-to-treat analyses are commonly used to counteract the effects of patient crossover but become invalid in the setting of excessive patient crossover. While no exact threshold of crossover percentage that invalidates a trial is known, with a 0% crossover being theoretically ideal and a 100% crossover rate completely invalidating a trial, the CEBM suggests a ‘‘rate of greater than 20% is a rough guide to the number that may invalidate the final results. ’’ The 70% rate of crossover in the current study, with patients crossing over on average less than 3 months after their surgical counterparts, is concerning and should be interpreted as a ‘‘fatal flaw’’ of the study. The outcomes of the physical therapy (PT) group in this study are heavily dependent on the outcomes (at all time points) of the majority of patients ultimately having surgery. This results in a comparison of a group in which 95% had surgery to a group where 70% had surgery. This is an unfortunate result of the current study design and setting. Other similar studies have made efforts to limit early crossover in this setting. The crossover rate of this study alone confounds the data and limits the reader’s ability to draw any significant conclusions. As a comparison, the METEOR RCT comparing arthroscopic partial meniscectomy to PT was criticized for a high rate of crossover (27%). The authors and reviewers of the study concluded that the lack of difference between the 2 groups in the setting of this crossover ‘‘suggest that an initial course of rigorous PT . may not compromise surgical outcome. ’’ This conclusion is perhaps better suited to the current study. Second, after crossover and loss to follow-up, only 11 patients remained in the PT group (compared to 63 for surgery). No data are provided to better understand if deterioration, no change, or another factor was the reason for crossover, which occurred on average less than 3 months after the surgical group, after the patients have evaluated their improvement after PT. The authors did perform an ‘‘as treated’’ or sensitivity analysis, in addition to the intention-to-treat analysis, and stated it ‘‘did not change the outcome’’ with no mention of the power of this comparison. However, in the ‘‘as treated’’ analysis, the advantages of the RCT are lost at this point, as shown in the significantly different characteristics of the patient groups (as seen in pain chronicity 62% vs 14%; no P value noted). In a trial comparing surgery and PT, the inclusion of patients from the surgery group (n = 2) who did not undergo surgery in the comparison group also doesn’t seem appropriate because they did not cross over to the structured PT group but rather had no intervention at all. With only 11 patients remaining in the actual PT group (35% of the number of patients needed based on power analysis), the study is at a high risk of type II error. Detailed assessment of the cohorts by established minimal clinically important difference (MCID) standards is not well reported in the current study; instead, the authors rely on the global rating of change (GRC) assessment tool. Most studies currently favor use of MCID change in PROs for assessing change due to the potential recall bias of GRC in remembering a health state several years prior. While ‘‘no statistically significant difference between the surgery and no surgery groups’’ was present, the surgery group demonstrated a significant increase in Hip Outcome Score (HOS) activities of daily living (ADLs), while a negative nonsignificant trend was present in the no surgery group. The results of this underpowered analysis are better described as ‘‘not finding a statistical difference’’ rather than ‘‘there being no difference’’ between the 2 groups. The external validity of RCTs is an additional important factor for the reader. In the current study, the single surgeon and military setting of the study should be considered. The military population has unique issues and challenges and is similar to a workers’ compensation population. The use of narcotic pain medication in both cohorts for an average of 16 months is concerning and not typical of most femoroacetabular impingement (FAI) patients. The PROs after surgery in this study are low compared with the multiple published reports on hip arthroscopy for FAI The American Journal of Sports Medicine 2018;46(8):NP35–NP39 2018 The Author(s)