Mobi-C for cervical disc replacement

Clinical and technical evidence

Costs and resource consequences

NHS Hospital Episode Statistics (HES) data indicate that in all English NHS hospitals in 2014/15, there were 4,642 finished consultant episodes relating to 'primary decompression operations on cervical spine' and 168 for 'revisional decompression operations on cervical spine' (revision rate of around 3.6%). The former description also includes 1,976 episodes of 'primary anterior decompression of cervical spinal cord and fusion of joint of cervical spine' (that is, discectomy plus fusion). This compares with 308 episodes of 'prosthetic replacement of cervical intervertebral disc' representing a ratio of discectomy plus fusion to cervical disc replacement of about 6:1 (Health and Social Care Information Centre 2015).

The manufacturer notes that Mobi‑C has been used for more than 2,000 procedures in the UK. The procedure is done in specialist spinal units, and more widespread use of the device is not expected to change service delivery if limited to these centres. The cost of prosthetic cervical disc surgery is greater than alternative ACDF surgery, so overall costs may increase if fusion surgery is replaced by Mobi‑C procedures. However, the use of Mobi‑C may result in savings if it can lead to a reduction in the number of adverse events, a reduction in the number of revision surgery procedures, and a reduction in the number of adjacent‑segment reoperations.

Strengths and limitations of the evidence

The systematic review by Alvin et al. (2014) was evaluated using the systematic review and meta‑analyses checklist recommended by the NICE guidelines manual. The systematic review was deemed to be of a relatively poor quality. The search strategy used was unsophisticated, given that only a basic set of search terms appeared to have been used (full strategy not reported) and only 1 database (MEDLINE) was searched. It was also unclear what process was adopted for sifting and data extraction, and whether 2 independent reviewers were involved in this process. For the studies that were included, no assessment of study bias took place, with the exception of a check for conflicts of interest. Within the review, included studies were classified by 2 independent reviewers according to the level of evidence. This assessment incorporated criteria defined by Sackett et al. (2000), which included an analysis of study factors such as length of follow‑up, percentage of subjects available at follow‑up, and reporting of outcome measures. Alvin et al. (2014) also addressed an appropriate and clearly defined question, and included relevant studies.

The 3 randomised controlled trials were evaluated using the checklist recommended in the NICE guidelines manual. Davis et al. (2015) presented 48‑month follow‑up results of an RCT in which the study design had been reported previously (Davis et al. 2013). Similarly, Hisey and colleagues (2016) presented 60‑month follow‑up results of an RCT in which the study design had been reported previously (Hisey et al. 2014). For both Davis et al. (2015) and Hisey et al. (2016), information from the underlying studies was used to assess the bias within each paper.

The risk of selection bias in Zhang et al. (2014) was unclear. The paper did not report the method of randomisation, and it was unclear whether there was adequate concealment of allocation for investigators and patients. Furthermore, although the authors noted that the demographics were similar between the 2 treatment groups, they did not report the numerical values for the different characteristics or whether tests for statistical significance were done. It was therefore unclear whether the groups were comparable at baseline. The risk of selection bias in Davis et al. (2013 and 2015) and Hisey et al. (2014 and 2016) was deemed to be low. In both studies an interactive voice randomisation system was used to appropriately randomise patients and divide them into subgroups based on NDI score. It was unclear whether there was adequate concealment of allocation for investigators and patients in both studies. In both studies the treatment groups were comparable at baseline, with no statistically significant difference in all characteristics reported.

All 3 studies were deemed to be at high risk of performance bias. In each study, the 2 treatment groups did not receive the same care aside from the intervention. In Zhang et al. (2014) the comparator group received a neck‑encumbering brace 48 to 72 hours after surgery, whereas the Mobi‑C group did not. The authors did not justify the difference between treatment groups, and it was unclear if this was a bias or if it accurately reflected standard practice. However, it appears likely that the difference could affect long‑term patient outcomes. Furthermore, it was not clear if patients were kept blind to their treatment. In both the Davis et al. (2013 and 2015) and Hisey et al. (2014 and 2016) studies, the care given after surgery was at the discretion of the surgeon, and this included a prescribed rehabilitation programme. Therefore, it is likely that the care differed depending on the surgeon who did the original procedure.

The Hisey et al. (2016) study included 25 surgeons across 23 sites. Davis et al. (2015) did not report exact surgeon numbers, but the trial took place over 24 sites so a similar number of surgeons may have been involved. It was not clear in either study how patients from the 2 treatment groups were allocated across the sites. In both studies the patients were blinded to allocation before surgery; however, allocation was revealed after surgery. It is not clear how this may have affected long‑term outcomes. Surgeons were not blinded to the allocation of treatment, but this was not possible due to the nature of the procedures.

The risk of attrition bias was low in Zhang et al. (2014) and unclear in Davis et al. (2015) and Hisey et al. (2016). Zhang et al. (2014) reported that all included patients were evaluated after surgery for a minimum of 48 months (the last time point assessed within the paper), so no drop‑outs were reported. In Davis et al. (2013 and 2015), both treatment groups were followed‑up for 28 months. However, 17 patients who were initially randomised did not have surgery, and outcomes data were unavailable at 48 months for 25 patients in the Mobi‑C group (11%) and 20 patients in the ACDF group (18%). It is not clear if this difference was statistically significant or not, because p‑values were not reported. The presence of any systematic differences between groups was also not reported, both in terms of those who did not have surgery compared with those who did, and those who were not followed up for the full 48 months compared with those who were. It appeared that all patients who were randomised in the Hisey et al. (2014 and 2016) study subsequently had surgery. Following surgery, 24 patients in the Mobi‑C group (14.5%) and 18 patients in the ACDF group (22%) did not remain in the trial for the full 5 year follow‑up period. It was not clear if the drop‑out rate was statistically significantly different between groups, as p values were not reported. Similarly, it was not reported if there were any systematic differences between the 2 groups.

The risk of detection bias in the 3 studies was unclear. All 3 had an appropriate follow‑up time that enabled patient outcomes to be recorded. Similarly, they each used precise outcomes definitions. In Zhang et al. (2014), 3 specific outcome measures were used to determine clinical outcomes and patient improvement: the Japanese Orthopaedic Association questionnaire, a visual analogue scale and the NDI. However, it should be noted that all 3 measures are questionnaire‑based and are therefore subjective. This makes them more susceptible to the introduction of bias because patients may consciously or unconsciously misreport their symptoms or outcomes. In both the Davis et al. (2015) and Hisey et al. (2016) studies, the overall rate of success was determined using a composite end point of 5 outcome measures: change in NDI from baseline, re‑operation rates, adverse event rates, neurological outcomes and radiographic success. Because positive results were needed for all 5 measures in order for the surgery to be considered a success, the risk of bias was very low. Within Davis et al. (2015) and Hisey et al. (2016) a number of secondary outcomes were also presented. For all 3 studies it was not clear if investigators were blinded to patient allocation. If investigators were not blinded they may have been able to influence patient responses on subjective measures, such as the NDI.

All 3 studies were done outside of the UK: Zhang et al. was based in China, and both Davis et al. (2013 and 2015) and Hisey et al. (2014 and 2016) were done in the US. The results may therefore have limited generalisability to the NHS. Furthermore, in both the Davis et al. and Hisey et al. studies the manufacturer of Mobi‑C contributed to the design and conduct of the study. The authors of the papers also disclosed financial interests, such as owning shares in the manufacturer or receiving research grants from the manufacturer. Therefore, funding bias may have been present.