Multicentre randomised controlled trial of the clinical and cost-effectiveness of a bypass-surgery-first versus a balloon-angioplasty-first revascularisation strategy for severe limb ischaemia due to infrainguinal disease. The Bypass versus Angioplasty in Severe Ischaemia of the Leg (BASIL) trial

BASIL audit

The aim of the audit was to determine the proportion of patients randomised into BASIL in relation to the total population of patients presenting with SLI, and to investigate the reasons for non-treatment and non-randomisation of potentially eligible patients. Over a 6-month period (October 2001 to April 2002), approximately halfway through the recruitment period, we prospectively gathered data on all consecutive patients who presented with SLI, and who subsequently underwent diagnostic imaging with a view to revascularisation by either bypass surgery or balloon angioplasty, at one of the six top-recruiting BASIL trial centres. In addition, the responsible consultant vascular surgeons and interventional radiologists were asked to record the reason(s) why, in their opinion, patients were deemed unsuitable for revascularisation or randomisation.

Trial eligibility, randomisation, procedures and follow-up

Participating centres were asked to invite all patients presenting with SLI [defined as rest (night) pain and/or tissue loss (ulceration, gangrene)] as the result of infrainguinal atherosclerosis and who, in the opinion of the responsible consultant vascular surgeon and interventional radiologist, required and were suitable for both bypass surgery and balloon angioplasty to take part in the trial.

All patients provided written informed consent and the study was approved by the Multi-centre Research Ethics Committee for Scotland. The BASIL trial was registered with the National Research Register and the International Standard Randomised Controlled Trials Number Scheme (ISRCTN45398889).

The trial manager, independently of participating centres, randomised patients to either a ‘bypass-surgery-first’ or a ‘balloon-angioplasty-first’ revascularisation strategy using a one-to-one ratio in randomly sized permutated blocks. The randomisation sequences were generated by a computerised random-number generator in the University of Edinburgh Medical Statistics Unit and supplied to the co-ordinating centre in sealed envelopes.

The referees requested that we respond to their criticism of the use of sealed envelopes: ‘Sealed envelopes have been established to be a poor choice of implementation of randomisation. Might be worth commenting that a future trial would use a centralised telephone/web-based randomisation system? Looking at Table 2, despite the authors’ reassurances, some of these differences look quite large for a trial of this size, e.g. current smoker 32% versus 40%, previous stroke 18% versus 25%, on antiplatelet 54% versus 62% etc. , and the sealed envelopes does make one wonder, probably needlessly, but nevertheless.’

In response, we respectfully submit that:

• sealed envelopes was standard practice when the trial was designed some 10 years ago

• the referees have picked out the extremes from small groupings

• adjusting for these small differences in the analysis made no difference to the results.

Randomisation was stratified by centre, and then by clinical presentation and ankle pressure, into four groups (Figure 1). 40,41

FIGURE 1.

Flow diagram of BASIL trial design.

Centres were encouraged to undertake the allocated procedure as soon as possible after randomisation. The responsible consultant vascular surgeons and interventionalists were permitted to use their normal practice for preintervention assessment, the procedure itself and aftercare. Follow-up data were collected prospectively by research nurses based in the main recruitment centres and allocated to other centres in the same UK region.

Details of patients recruited in Scottish centres were logged with the Information and Statistics Division (ISD) of the NHS in Scotland. Notification of death, interventions and discharges from hospital to the end of the trial were provided by using record linkage to Scottish Morbidity Records (SMR1) and General Registrar Office (Scotland) [GRO(S)] death records. Similar information was collected for patients from English centres using data from the Office for National Statistics (ONS) and patient-reported information, which was checked through paper hospital records, electronic hospital information systems and general practitioners. In addition, this prospectively gathered information was cross-checked by reviewing hospital case notes of trial patients at the end of the study.

The primary end point was amputation (of the trial leg at transtibial level or above) -free survival (AFS) and the secondary end points were overall survival (OS) [also known as ACM], post-procedure morbidity and mortality, reinterventions, HRQoL and the use of hospital resources.

The reviewers/editors have requested that we specifically respond to their concern regarding the rationale for including death from any cause as a component of the primary end point (AFS). They ask if nearly all the deaths are related to the underlying disease process being studied (i.e. SLI). They comment further ‘Naively, usually relevant cause-specific death is included and non-relevant deaths are either censored at the time of death; or possibly a competing risks type approach is considered?’

We respond as follows. It was decided in about 1998, when the trial was first designed, to include ‘all-cause mortality’ as an end point because it was considered likely to be a discriminator between the two treatment strategies. That decision has been vindicated by the trial data now available some 10 years later. We would respectfully suggest that ‘all-cause mortality’ is a more robust, reliable and relevant end point than ‘cause-specific mortality’. AFS is the standard end point used in SLI trials (see Chapter 10) and is mandated by the Federal Drug Administration of the USA. Furthermore, competing risk approaches have been criticised as less clinically meaningful in this patient group, many of whom suffer from multiple life-threatening comorbidities.

The reviewers/editors have requested that we respond to their suggestion that ‘it is not always clear enough how the authors have dealt with deaths in the secondary outcomes – for example, in the patient-reported outcomes, the deaths seem to have been omitted. Now clearly they will not have values, but it is quite usual to impute floor values or the lowest possible state for those that have died – otherwise the analyses could potentially be biased if there are any imbalances in deaths between the groups.’

This is discussed at greater length in Chapter 7; however, here we respond as follows:

• we believe the methods we have used are more transparent and more relevant to clinical outcomes

• although a potential for bias is always possible it is much lower in a randomised study than might be the case in an observational study because the censoring pattern is the same in both groups

• additionally, in this particular study, any bias would be minimal because mortality differences were small

• the adjusted survival data are used in the calculation of quality-adjusted life-years (QALYs) (taken out to 3 years).

• a standard multiplicative model was used which allows for the utility value reported for each surviving time interval.

Data Monitoring Committee

An independent Data Monitoring Committee met every 6 months during the randomisation period. Having agreed that the stopping rule should be the observation of a highly significant difference in the primary end point (AFS) between the treatment groups (p < 0.001), the Data Monitoring Committee agreed to review the trial data 6-monthly, which were prepared for them by independent statisticians, and to make a recommendation to the Steering Committee as to whether the trial should continue. The Data Monitoring Committee also made recommendations to the Steering Committee on the nature and the quality of the data being collected.

Move of trial centre

The reviewers/editors have asked us to respond to their concerns regarding the move of trial office partway through the trial. Specifically, they have commented ‘The trial office seems to have moved from Edinburgh to Birmingham midstream. This happens sometimes, particularly in long trials. What were the issues and how where they overcome? This might be worth a section for the benefit of others facing the same issue.’

We respond as follows. Actually, while somewhat ‘inconvenient’ in the short term (it probably put the trial back 6–12 months), the move increased the availability of patients from English centres and this made the trial possible. Had the trial remained confined to Scotland (as was originally envisaged) it is unlikely that we would have recruited the number of patients deemed necessary by the power calculation in the time available. The learning point is to engage the largest population (centres/patients) possible from the outset (i.e. always recruit on a national and, if possible, international basis). Such an approach also increases generalisability across the UK; of course at the expense of homogeneity. This tension between inclusivity and purity exists in every large pragmatic RCT and can never be resolved to everyone’s satisfaction (this is discussed further in Chapter 10).

Statistical analysis

The sample number calculations proposed that 223 patients per treatment arm would be needed for a 90% power to detect a 15% difference in 3-year AFS at the 5% significance level. This was based on the assumption that the 3-year AFS in one group might be 50% and that in the other group it might be 65%. As discussed above, the primary end point was reached when the trial leg underwent amputation at transtibial level or above (partial foot and digital amputations were not counted as primary end points) or when the patient died of any cause, whichever was sooner. Kaplan – Meier methods were used to construct survival curves on an intention-to-treat basis, using the date of randomisation as time zero.

The statistical analysis was carried out according to a predefined protocol. Survival to the primary end point (amputation of the trial leg or death, AFS) and a secondary end point (ACM or OS) were to be compared by intention to treat. Treatment comparisons were to be survival to 1 year and 3 years from randomisation and hazard rates using a Cox model. The hazard rates were to be compared over the whole time period and separately for events occurring in the first 6 months from randomisation and in the period from 6 months onwards and would be adjusted for a predefined set of covariates. Covariate interactions with treatment would be examined for three specified covariates (stratification group, diabetes and creatinine above/below the median) and also for a risk score calculated from covariates that classified patients according to their hazard of experiencing an end point. All data cleaning and checking of the follow-up data were carried out without reference to the allocated treatment. After the survival curves were examined a further post-hoc analysis was carried out that compared the hazards of the end points restricted to the period after 2 years from randomisation.

Health-related quality of life

We measured self-reported HRQoL using the VascuQoL, EuroQoL 5-D (EQ-5D)42 and the Short Form 36 (SF-36). 43 These generic measures were collected at baseline (before randomisation) and at 3, 6 and 12 months after randomisation. The EQ-5D responses were converted into a single weighted utility (preference-based) score using the original time trade-off tariff set. 44 The SF-36 items were combined into physical and mental component summary scores using recommended procedures. 45 For all three measures, higher scores indicate better health and well-being as perceived by the patient. Unadjusted differences in mean EQ-5D weighted scores and SF-36 component summary scores were assessed using simple linear regressions. Adjusted differences allowing for baseline scores were based on bias-corrected matching estimators. 46 Further detail on HRQoL methods and analysis is presented in Chapter 6.

Inpatient hospital use and cost

We obtained data on first and all subsequent interventions and hospital stays during follow-up. Patient-specific hospital use was measured using the duration of hospital stay as an aggregate unit of services provided in the inpatient hospital setting. Total length of hospital stay was measured for 1 year from the date of randomisation. Hospital use was valued using the average cost per inpatient day using the Scottish system of hospital cost statistics. 47 The inpatient hospital cost per day was estimated at £421 for vascular surgical days, £591 for high-dependency unit (HDU) days and £1526 for intensive-therapy unit (ITU) days. The average procedure costs of bypass surgery (£3104) and balloon angioplasty (£1159) were based on estimates in a recent HTA review. 48 Inpatient costs per day and procedure costs are reported on a price base of financial year 2003–4. Further detail on HRQoL methods and analysis is presented in Chapters 3 and 7.

BASIL audit

This was a prospective audit to determine the numbers of patients presenting with SLI; the proportion of those who were eligible for randomisation within the trial and the proportion of those who were randomised. We also wished to collect data on those who were considered ineligible for randomisation and why; and on those who were considered eligible but were not randomised and why. It was decided for logistical reasons to undertake this audit in the centres that had recruited the most patients to the trial. We decided to conduct the audit approximately halfway through the recruitment period to try to offset any changes in practice, and attitudes to the trial, that may have occurred over this time.

Over a 6-month period (October 2001 to April 2002), approximately halfway through the trial recruitment period, 585 consecutive patients presented with SLI to the top six recruiting centres (who between them recruited 61% of the patients entered into the trial) and underwent diagnostic imaging, usually angiography, with a view to consideration of revascularisation by either bypass surgery or balloon angioplasty (Figure 2). Of these, 129 (22%) required suprainguinal (aortoiliac) intervention and were not, therefore, the subject of the BASIL trial. Of the remaining 456 patients [272 men and 184 women of median (range) age 75 (33–99) years] with SLI due to infrainguinal disease, 220 (48%) were treated conservatively initially without immediate/early revascularisation and 236 (52%) were deemed to require, and be willing to undergo, immediate/early revascularisation. Of these 236 patients, 70 (29%) were considered suitable for randomisation into the BASIL trial because the responsible surgeon and interventionalist agreed that there was equipoise with regard to the preferred first intervention. For the other 166 patients there was a clear preference on the part of the responsible vascular team, or expressed by the patient/family, for either bypass, or angioplasty, or continuing conservative therapy or primary amputation. The responsible consultant vascular surgeons and interventionalists stated that the primary reason for not revascularising or not randomising patients (n = 386) was that: the leg could not be revascularised by either bypass surgery or balloon angioplasty (n=154, 34%) (non-reconstructable disease); there was significant comorbidity precluding bypass surgery (n=34, 7%); there had been symptomatic improvement with medical therapy only (n=14, 3%); the patient was unable to provide informed consent (n=16, 4%); the patient’s pattern of disease was technically unsuitable for balloon angioplasty (n=75, 16%) or bypass surgery (n=93, 20%). Note that in many patients there was more than one reason and in many cases the decision was influenced by patient/family wishes. Of the 70 patients deemed suitable for randomisation, 22 refused trial entry and 48 (69%) were randomised.

FIGURE 2.

BASIL trial audit: CONSORT diagram showing patient flow into trial.

Trial recruitment, randomisation and follow-up

Consultant vascular surgeons and interventional radiologists from 27 UK hospitals entered 452 patients into the study. A total of 195/228 (86%) patients randomised to bypass surgery and 216/224 (96%) randomised to balloon angioplasty underwent an attempt at their allocated treatment at a median (inter-quartile range) of 6 (3–16) and 6 (2–20) days respectively (not significant, NS). The baseline characteristics of the patients in each group were similar and typical of patients presenting with SLI (Table 2).

Over 40% of the patients were known to have diabetes and over one-third admitted that they were still smoking at the point of randomisation. The great majority of patients had tissue loss and one-quarter had both legs affected by SLI, indicating the advanced nature of the peripheral arterial disease in the trial population. Many of the patients were elderly and most had a significant cardiovascular past medical history. Despite this, one-third of patients were not receiving an antiplatelet agent and only one-third of the patients were receiving a statin at the time they were referred to the vascular service.

The trial ran initially for 5½ years (see Chapter 3 for reporting of extended follow-up). By the close of follow-up on 28 February 2005, 99% of patients had been followed up for 1 year, 74% for 2 years, 48% for 3 years, 22% for 4 years and 8% for 5 years. At the end of this initial (interim) follow-up, 248 (55%) patients were alive with their trial leg intact, 38 (8%) were alive with their trial leg amputated, 36 (8%) had died subsequent to having their trial leg amputated and 130 (29%) had died with their trial leg intact.

Post-procedure (30-day) morbidity, mortality and reintervention

Six patients randomised to bypass surgery and one randomised to balloon angioplasty died before undergoing an intervention. Eleven patients randomised to bypass surgery (5%) and seven to balloon angioplasty (3%) died within 30 days of their first intervention. One patient in each randomised group crossed over and died within 30 days of the alternative procedure so that the 30-day mortality associated with each procedure was the same whether analysed by intention to treat or by first treatment received. A total of 110/195 (57%) patients who were randomised to and underwent attempted bypass surgery as their first procedure and 89/216 (41%) patients who were randomised to and underwent attempted balloon angioplasty as their first procedure had one or more complications within 30 days of their intervention (Table 3). Of these 89 patients, 20 did not develop their complication until after they had gone on to have bypass surgery as a second procedure after a failed balloon angioplasty as a first procedure.

Patients randomised to surgery: early (12-month) follow-up

Of the 228 patients randomised to bypass surgery, 195 underwent attempted bypass surgery (Figure 3). Of these, five underwent a successful endarterectomy and vein patch rather than a bypass. Two bypasses were abandoned; one because the surgeon considered the vessels were too calcified to construct a distal anastomosis and one because the surgeon could not find sufficient usable vein for a conduit and did not want to use a prosthetic graft. In a further three cases a graft was inserted and the operation was completed but in the opinion of the responsible consultant surgeon undertaking the procedure the bypass was not working at the end of the procedure. The immediate failure rate was, therefore, 5/195 (2.6%). Consequently, 193 (84%) patients randomised to bypass surgery underwent a completed surgical procedure as their first intervention, of which 188 were completed bypasses (Table 4).

FIGURE 3.

CONSORT trial profile of patients randomised to bypass surgery (BSX): early (12-month) follow-up.

*Clinical failure of an intervention is defined as death, amputation of trial leg, return or persistence of symptoms (rest pain/tissue loss), whether or not further intervention is required, by 12 months from randomisation. **Clinical success of an intervention is defined as patient alive with trial leg intact without further intervention at 12 months.

Figures in italics describe all patient events (BAP, balloon angioplasty; BKA, below-knee amputation; AKA, above-knee amputation; D, death; NI, no intervention) during the first 12 months from randomisation in patients allocated to bypass surgery. A dash is used to separate the stages. So, for example, in the box entitled ‘Clinical failure of second intervention (n = 7)’ the phrase ‘BSX-BSX-D (1)’ means that one of those seven patients had further surgery (third intervention), then more surgery (fourth intervention), and then died.

In addition, four patients who had been randomised to balloon angioplasty underwent successful bypass surgery as their first intervention. By 12 months, 85/195 attempted bypass surgeries had resulted in clinical failure defined by death (n = 29), major amputation (n = 20) or a return or persistence of symptoms (rest pain, tissue loss) in the trial (operated) leg or the finding of a technical problem with the graft on surveillance (n = 36). Of the last group, 33 proceeded to have a second intervention, which in most cases was balloon angioplasty. A number of patients randomised to bypass surgery went on to have further interventions, amputation or to die within 12 months of randomisation as shown in Figure 3.

Patients randomised to balloon angioplasty: early (12-month) follow-up

Of the 224 patients randomised to balloon angioplasty, 216 underwent attempted balloon angioplasty (Figure 4).

FIGURE 4.

CONSORT trial profile of patients randomised to balloon angioplasty (BAP): early (12-month) follow-up.

*Clinical failure of an intervention is defined as death, amputation of trial leg, return or persistence of symptoms (rest pain/tissue loss), whether or not further intervention is required, by 12 months from randomisation. **Clinical success of an intervention is defined as patient alive with trial leg intact without further intervention at 12 months.

Figures in italics describe all patient events (BSX, bypass surgery; BKA, below-knee amputation; AKA, above-knee amputation; D, death; NI, no intervention) during the first 12 months from randomisation in patients allocated to balloon angioplasty. A dash is used to separate the stages. So, for example, in the box entitled ‘Requiring further (third) intervention (n = 9)’, the term ‘BSX-BSX-BKA (2)’ means that of those who require a third intervention two patients had further surgery (third intervention), then more surgery (fourth intervention), then a BKA (fifth intervention). Then, because there is no ‘-D’ at the end these two patients were alive at 12 months after randomisation.

In the opinion of the vascular interventional radiologist undertaking the procedure, 43 (20%) of these were immediate technical failures. In 10 cases this was because the vessel lumen could not be entered or the disease could not be completely crossed with a guide-wire. In 18 cases the lesion was crossed subintimally but the lumen could not be re-entered. Two procedures were abandoned before a guide-wire had been passed across the disease because the patient could not tolerate the procedure. Two procedures were terminated because of vessel perforation after a guide-wire had been passed. One procedure was terminated immediately because the disease described as being present on preoperative duplex ultrasound was found not to be present at the time of angiography. In a further 10 cases there was immediate thrombosis of the balloon angioplasty channel and in six of those cases there was also distal embolisation that could not be rectified radiologically by means of either thrombolysis or aspiration. The anatomic extent and type of balloon angioplasty performed in the 203 patients undergoing attempted balloon angioplasty, and in whom a guide-wire was passed across at least part of the disease to be treated are shown in Table 5. In addition, 21 patients allocated to bypass surgery crossed over and underwent attempted balloon angioplasty as their first intervention; of these, five were immediate failures.

By 12 months, 109/216 (50%) attempted balloon angioplasties had resulted in clinical failure as defined by death (n = 21), amputation (n = 16) or a return or persistence of symptoms (rest pain, tissue loss) (n = 72) in the trial leg. Of these, 59 proceeded to have a second intervention, which in most cases was bypass surgery. A number of these patients went on to have further interventions, amputation or to die within 12 months of randomisation as shown in Figure 4.

Comparison of reinterventions following bypass surgery and balloon angioplasty

Following randomisation to, and attempted, bypass surgery, 109/195 (56%) patients were alive with the trial leg intact at 12 months without further intervention. This compares with 107/216 (50%) patients following randomisation to, and attempted, balloon angioplasty. Looking at the follow-up as a whole by intention to treat, bypass surgery was associated with a lower reintervention rate (41/224, 18.3%) than balloon angioplasty (59/228, 25.9%); a difference of 7.6% (95% CI 0.04% to 15.12%). When analysed by the first intervention received, the difference between reintervention following bypass surgery (33/199, 16.6%) and balloon angioplasty (67/237, 28.3%) was greater; a difference of 11.7% (95% CI 3.9% to 19.2%).

Survival to primary end point (AFS) and secondary end point (ACM)

Figures 5 and 6 show Kaplan – Meier survival curves to the primary end point (AFS) and the secondary end point (ACM), also known as overall survival (OS).

FIGURE 5.

Amputation-free survival following bypass surgery and balloon angioplasty by intention to treat (2005 analysis).

FIGURE 6.

All-cause mortality following bypass surgery and balloon angioplasty by intention to treat (2005 analysis).

Survival to the primary end point at 1 and 3 years was 68% and 57% for those randomised to a bypass-surgery-first strategy and 71% and 52% for those randomised to a balloon-angioplasty-first strategy. There were no significant differences in survival to either end point by randomised group. Hazard ratios (HRs) comparing randomised treatments by Cox proportional hazards are given in Table 6.

None of the planned comparisons provided strong evidence of a difference between the treatments. However, up to 6 months, there was a trend towards an increased hazard with bypass surgery relative to balloon angioplasty in terms of ACM, whereas after 6 months there was a trend towards a reduced hazard with bypass surgery in terms of AFS and ACM. A post-hoc analysis, carried out following examination of the survival curves, found a significantly reduced hazard in terms of AFS [adjusted HR 0.37 (95% CI 0.17 to 0.77), p = 0.008] and ACM [adjusted HR 0.34 (95% CI 0.17 to 0.71), p = 0.004] for bypass surgery relative to balloon angioplasty in the period beyond 2 years from randomisation. There was no evidence of differential effectiveness of the interventions from the treatment by covariate interactions for either end point overall or in any of the time periods. The covariates with the strongest independent influence on survival to the end points were stratification group, diabetes, creatinine and age.

HRQoL results

At baseline the two treatment groups were balanced in terms of HRQoL. Patients in both treatment groups reported improved EQ-5D and SF-36 physical component summary scores by 3 months which were largely sustained during follow-up. However, little further improvement was observed beyond 3 months (Table 7). There was also improvement over a longer time period in the SF-36 mental component summary score. Although there is weak evidence that HRQoL may be somewhat better in the surgery group, there are no significant differences in HRQoL when the two treatment groups are compared. This finding is consistent across the three HRQoL scores.

Use of hospital resources

The use of hospital resources by the two groups on an intention-to-treat basis during the first 12 months from randomisation are compared in Table 8. There was no difference between the bypass-surgery-first and the balloon-angioplasty-first strategies in terms of the number of hospital admissions. However, patients randomised to bypass surgery spent significantly longer in hospital and required significantly more HDU and ITU care than those randomised to balloon angioplasty. Indeed, 23% of patients randomised to bypass surgery required HDU and 4% required ITU care during the first 12 months of follow-up compared with 0.5% and 7% of patients randomised to balloon angioplasty.

The mean cost of inpatient hospital treatment during the first 12 months of follow-up in patients randomised to a bypass-surgery-first strategy has been estimated as £23,656 (£20,431 hospital stay and £3225 procedure costs), which is approximately one-third higher than the £17,496 (£15,457 hospital stay and £2039 procedure costs) for patients randomised to a balloon-angioplasty-first strategy.

Statistical analysis

The power to detect an HR of 0.5 for bypass surgery versus balloon angioplasty from new events (amputation, death) after 2 years from randomisation was estimated at 90% with p = 0.05. This was based on a simulation study using a Weibull parametric survival model using separate hazards before and after 2 years from randomisation. As the expected direction of difference was known, a one-sided test was specified and agreed by the funding body (HTA). However, the decision to use a one-sided test has been questioned by the reviewers. We respectfully suggest that the decision to use a one-sided or two-sided test depends on the action that would be taken in response to a finding. The purpose of a significance level is to control the level of false positives. A one-sided test should only be carried out if it would be certain that, had the results gone in the other direction, no matter how strongly, they would not be interpreted as anything other than chance. In planning the protocol for further follow-up we, and the funding body (HTA), felt that this would apply here.

The second (2008) statistical analysis was conducted according to a prespecified protocol that was finalised before the further follow-up data (2005–8) were available (see full statistical plan in Appendix 2).

A Cox proportional hazards model was used to examine survival to the primary (AFS) and secondary (OS) end points. For the survival analyses, patients with no report of death were taken as censored at the end of February 2007 if their death information was from ISD, as censored at the end of July 2007 if their death information was from the Office for National Statistics (ONS), or at the date of last clinical contact if it was after this date. In addition, four patients who were lost to follow-up and who were thought unlikely to have their deaths recorded in the UK were censored at their last follow-up times; all within 1 year and 1 month of randomisation. An analysis was undertaken to evaluate new information from the additional follow-up since the 2005 analysis, highlighting the period 2 years beyond randomisation. The protocol stated that ‘If this additional data, by itself, provides evidence of a higher event rate for those assigned to bypass (one-sided test) then it will be strong evidence that the previously identified trend was not due to chance.’

The reviewers have suggested that using updated values of covariates at 2 years post-randomisation might have given a more complete adjustment for the non-randomised comparison between surgery and angioplasty. It is further suggested that one would clearly expect (1) the baseline covariates to be less predictive 2 years on and (2) potentially substantial differences not just in the baseline covariates of those left at 2 years but even more so in the updated values – hence leading to a better adjustment of the treatment effect. However, we did not feel it was appropriate to adjust for post-randomisation covariates as they could have been affected by treatments, and hence could give a biased result that would be difficult to interpret. For example, were we to use some measure of fitness at 2 years (e.g. ankle pressures) it might have been the effect of one treatment on this that had the result of improving survival. However, if we were wrongly to adjust for this the real benefit of this treatment would not be apparent.

For the HRQoL analysis descriptive statistics were based on completed baseline and follow-up questionnaires with no missing items. VascuQoL and EQ-5D weighted scores were assessed using simple linear regressions. Adjusted differences allowing for baseline scores were based on bias-corrected matching estimators. 46 The full sample method was used to summarise the cumulative distribution of hospital costs arising from the time of randomisation to follow-up (3 years) using arithmetic mean costs observed for all patients. Confidence intervals for estimated untransformed arithmetic mean costs were estimated analytically and empirically using bootstrapping techniques to check for the adequacy of the assumptions made regarding the normality of the cost distributions. 55 We found that standard t tests and t test-based confidence intervals were very similar to those based on the bootstrap.

Overview

The BASIL trial methods have been described in Chapters 2 and 3 and published elsewhere50 and the clinical end points were AFS (i.e. patient alive without amputation of trial leg at transtibial level or above) and OS. Detailed clinical data were collected at baseline (see trial forms in Appendix 3) and the preintervention angiograms were scored according to the Bollinger method (infrainguinal segments) and the TASC II criteria (see Chapter 6). 51,52

Statistical analysis

For the survival analyses patients with no report of death were taken as censored at the end of February 2007 if their death information was from the ISD, at the end of July 2007 if their death information was from the ONS, or at the date of last clinical contact if it was after this date. In addition, four patients who were lost to follow-up and who were thought unlikely to have their deaths recorded in the UK were censored at their last follow-up times; all within 1 year 1 month of randomisation. The potential predictors that were used in the survival analyses were all measured at the time of randomisation, before the patients’ assigned treatments were known. The initial set of predictors selected included those that were specified as covariates in the trial protocol. For these predictors we undertook descriptive, univariate and multivariate analyses within a Cox proportional hazards model.

Parametric survival model for up to 2 years from the decision point

To predict how a future patient might behave in terms of OS up to 2 years from randomisation a parametric survival model was developed. Only survival up to 2 years from randomisation was used, with all survivors beyond this time censored at 2 years. This model used the predictors defined in the protocol and a further set of four variables identified in the baseline data that were considered as potential predictors. A simpler model was obtained from these potential predictors by a combination of backward selection and the plausibility of the associations revealed. This approach runs the risk of over-fitting the model, such that the predictions are more extreme than are justified by the data. To overcome this, the model was developed on a training data set which consisted of a randomly selected 75% of the original data. A shrinkage factor was then calculated that corrects the model for over-fitting, and the predictions were validated on the remaining 25% of the data. A similar approach could have been used for AFS and the results would have been very similar in terms of the ordering of the prognostic factors identified. A Weibull parametric survival model was used because it has a hazard function that can either increase or decrease with time from randomisation (please see below). Specifically, the Weibull model estimates a shape parameter and a linear predictor which together can be used to calculate the predicted survival to a given time for any combination of baseline characteristics. The probability of surviving to time t can be written as , where s is the shape parameter and η is a linear predictor calculated from the baseline characteristics. A shape parameter of 1.0 gives a model with constant hazard (exponential distribution of survival times) while a shape parameter below 1.0 indicates a hazard that is decreasing over the follow-up period.

Amputation-free survival and overall survival

The numbers of amputations and deaths before and after 2 years from randomisation are shown in Table 14.

Figure 10(a) shows the survival curves for all patients to amputation or death, or to death. After the first 1–2 years of follow-up the two curves are fairly parallel, indicating that there are few new amputations at this length of time from randomisation.

The smoothed estimates of the hazard functions (Figure 10b) show that the number of amputations in the first year and a half increases the ‘amputation or death’ hazard compared with that for death only, whereas after that time there are few extra amputations to increase the hazard of ‘amputation or death’ compared with death. Note also that the initially very high hazards for both end points decline over the first 2 years and appear to become fairly constant after the first 2 years.

FIGURE 10.

Amputation-free survival (primary end point) and overall survival for whole BASIL trial cohort presented as (a) survival curves and (b) smoothed hazard for each event. The vertical lines on the survival curve (a) indicate that an observation is censored. PEP, primary end point = amputation-free survival (i.e. amputation or death, whichever comes first).

This reducing risk is shown by the numbers of amputations during follow-up: 61, 5, 7, 3 and 3 in years 1 to 5, respectively.

Relationship between overall survival and baseline clinical factors

The results of the univariate and multivariate Cox proportional hazard models for AFS and death from any cause over the whole follow-up period are shown in Tables 15 and 16. The baseline factors that remained significant for OS in the multivariate Cox model were in descending order of importance:

• BASIL randomisation stratification group

• below-knee Bollinger scores

• body mass index (BMI)

• age

• diabetes, type I and type II together

• creatinine

• smoking.

The survival curves to death by each of these factors is shown in Figure 11(a to g) and Figure 11(h) shows the survival by randomised treatment on the same scale for comparison. In most cases the association of the factors with survival was in the expected direction and was similar in the univariate and the multivariate analyses. The exceptions were BMI and smoking. A high BMI was associated with better survival in both the univariate and multivariate analyses. In the univariate analysis current smokers had survival similar to never smokers and ex-smokers had poorer survival but in the multivariate analysis the association was as expected with the current smokers and ex-smokers both having worse survival than non-smokers. This further supports the suggestion that the ex-smoker category has a favourable predicted survival from other factors that improves their survival in the univariate analysis. The time dependence of each of the covariates was checked in the multivariate model using a test for the correlation of the weighted residuals with time. 57 The above-knee Bollinger mean angiogram score was the only factor to show time dependence but the effect was small and probably a false-positive result, given the large number of effects examined.

FIGURE 11.

Survival to death by baseline covariates. (a) BASIL randomisation stratification group; (b) mean below-knee Bollinger angiography score; (c) body mass index; (d) age; (e) diabetes types 1 and 2 together; (f) log serum creatinine; (g) smoking status; (h) treatment allocation at randomisation. AP, ankle pressure.

The effect of randomised treatment

The significant survival advantage, after 2 years, for patients randomised to surgery can be seen in Figure 11(h). The opposite is true in the earlier period, although this was not a significant difference. For the whole time period the test for a time-dependent hazard was significant at p = 0.028. 57 This suggests that, given the current evidence, the clinical decision as to whether surgical or radiological treatment is more appropriate should be guided by the chances of the patient’s surviving for more than 2 years. We have developed a model that looks at this directly. Compared with the effect of the other covariates the effect of randomised treatment is small and for all practical purposes can be ignored for predicting survival up to 2 years. The randomised treatment was not, therefore, included in the prognostic model.

The reviewers have questioned the decision to omit randomised treatment from the model. They suggest that it is not a question of significance in the data set at hand, it is a structural component in the data, and should really be included. We considered its inclusion when we were planning this analysis but, as described above, because the effect of treatment was so small compared with that of other factors, we decided that it would be simpler to omit it from the model. We did check this assumption post hoc and found that having included treatment made almost no difference to the ranking of cases.

The reviewers have raised some concerns about the amount of missing data. They ask how this arose and what we did analysis-wise; they suggest that if this was a complete case only, then the cumulative missingness across all these variates could have led to a substantial deletion of subjects in the models. We agree that the level of missingness is quite high in certain areas although overall we believe that the completeness of the data compares favourably with other studies in this field. In the analysis a missing data category was used for variables with a substantial amount of missing data. This approach has been criticised when the focus of interest is the covariate, but where it is being used as an adjustment it is, we respectfully suggest, considered an acceptable approach.

Modelling overall survival to 2 years from randomisation

The baseline data described above that were used to adjust for the effect of treatment in the main end point analysis (see Chapters 2 and 3) were further examined to determine if there were any other factors that could improve the predictive model. Three further factors were selected:

• number of ankle pressures measurable using hand-held Doppler ultrasound

• a history of myocardial infarction or angina

• a history of stroke or transient ischaemic attack.

With regard to the first of these, examination of the ankle pressure data showed that there were many cases where one or more of the three possible ankle pressures (dorsal pedis, posterior tibial and peroneal) were classed as ‘not recordable’. In general, as might be expected, there was a positive relationship between a low ankle pressure and ‘missing’ ankle pressures (Table 17).

Figure 12(a) illustrates the survival to death curves up to 2 years by the number of ankle measurements obtained. The final ankle pressure was defined in the protocol as the maximum of the values obtained. Figure 12(b) shows the survival to death by a finer grouping of the pressure values for those where a measurement was possible.

FIGURE 12.

Overall survival to 2 years by (a) number of ankle pressures measurable using hand-held Doppler ultrasound, (b) highest ankle pressure measurable (mmHg), (c) history of myocardial infarction (MI) or angina, and (d) history of stroke or transient ischaemic attack (TIA).

The stratification indicator at randomisation was replaced by these two ankle pressure measures (the highest ankle pressure obtained and the number of measurements obtained) and whether tissue loss was present (considered separately). The number of ankle pressure measures was considered as an unordered category. The two clinical histories (myocardial infarction or angina, stroke or transient ischaemic attack) were added as possible contributors to the prognostic model. Statin use was excluded because although in the BASIL trial only approximately one-third of patients were on cholesterol-lowering therapy, in 2009 almost all patients with SLI would be prescribed a statin as part of ‘best medical therapy’. 3 TASC II and the Bollinger above-knee angiography score were excluded as the below-knee Bollinger score was the stronger independent predictor.

Figure 12(c,d) illustrates the OS to 2 years by a history of myocardial infarction/angina or stroke/transient ischaemic attack.

A parametric overall survival model for up to 2 years from the decision point

A training data set was selected that consisted of a random selection of 75% of the original data (339 cases, 98 deaths) leaving the other 113 cases (33 deaths) to form a validation data set. When the data set is of limited size, the choice of which proportions to use in the training and validation data sets is difficult. A training set with too few cases may yield a poor prediction and a validation data set with too few may make the interpretation of the validation results difficult. We decided that the former was more important and so selected a larger training data set.

Starting with all the variables mentioned above, we attempted to find a simpler model that might fit the data better.

The procedure was to use backward elimination with the option to remove any variables for which the grouped p-value (for categories) was greater than 0.1. However, each case was considered in terms of the plausibility of the coefficients for the individual groups and retained if these seemed clinically reasonable and important. Continuous variables replaced groupings where effects appeared linear.

One particular decision is worth highlighting. The ankle pressure data were initially fitted as two categorical variables as illustrated in Figure 12. With all the other variables in the model the groups for ankle pressure did not approach statistical significance. However, the coefficients for the groups showed a clear dose – response relationship, with the lowest group having the worst survival. It was therefore decided to include the ankle pressure in the model as a continuous variable, because of its clinical plausibility, even though its p-value (two-sided) for including in the final model was only 0.25. Formally the ankle pressure value was replaced with zero when no measurements were taken, but the choice of value for those not measured does not affect the prediction when the number of ankle pressure measures is included in the prediction model.

The final model differed from the full model in that:

• Age was fitted as a continuous variable (range 39 to 99 years in the BASIL cohort).

• The number of ankle pressure measurements obtainable (range 0–3) was fitted as a categorical variable.

• The ankle pressure was taken as a continuous variable, set to zero if no pressure available.

• Below-knee Bollinger angiography scores were simplified to an average value < 5 or ≥ 5.

• Diabetes was excluded since it was no longer predictive once all the other variables were included.

The coefficients in the linear predictor for the training data set and the full data set are given in Table 18.

Model validation

When data are used to select a model the predictions will tend to be too extreme. We can correct for this by shrinking the individual predictions towards the mean. A very reasonable approximation to an appropriate shrinkage can be obtained by calculating a shrinkage factor as discussed by Copas. 58 This is calculated as [1 – (df –2)/k], where ‘df’ is the residual degrees of freedom used in fitting the model and k is the overall value of the chi-squared statistic for the final model. The linear predictors are then shrunk towards the mean value for the linear predictor by this factor. For this example a shrinkage factor of around 0.75 is obtained. We can check how well this shrinkage factor will correct any over-fitting by examining the fit obtained for the validation set. Linear predictors for the fitted model were obtained for the training and validation data sets and in each case three equal-sized groups were formed to make high, medium and low groups.

Figure 13(a) compares the modelled survival for the three groups based on the training data with the empirical survival curves. The fit is excellent. For the smaller validation data set the fit is poorer, as we would expect, and in particular it is too optimistic for the groups with good survival (Figure 13b). The shrunken estimates (Figure 13c) correct this. Although they appear to under-fit the poor prediction group, this could just be a chance effect because of the small size of the prediction data set. We recommend the shrunken predictor, with a shrinkage factor of 0.75 be used for individual predictions.

FIGURE 13.

Fits (a) training data, (b) validation data and (c) validation data with shrinkage. In each case the data were grouped into three equal-sized groups according to the value of the linear predictor. The dotted lines show the fitted Weibull survival for the average linear predictor in each group. The solid lines are the Kaplan – Meier survival curves for each group.

Predicting overall survival for future individual patients: a parametric overall survival model for up to 2 years from the decision point

Figure 14 shows a histogram of the probability of surviving to 2 years for the 452 patients randomised. We can see that, although there is a wide spread of probabilities of surviving to 2 years there are substantial numbers with a good prognosis. In particular, 52% of patients have a probability of survival to 2 years of 0.75 or more and 21% above 0.85. At the other extreme 19% of patients have a probability of less than 0.6 of surviving to 2 years based on their baseline characteristics.

FIGURE 14.

Histogram of the probability of surviving to 2 years (shrunken estimate), 452 randomised patients.

The information in Table 18 and the shrinkage factor can be used to calculate an individual linear predictor for any combination of covariates. Although the model was developed and validated from the training data set, it would seem sensible to make predictions for future patients from all the data available. This linear predictor can then be shrunk towards the mean of the all the predictors which has a value of 2.52 for prediction from the full data. The formula for the shrunken predictor then becomes 2.52+0.75 × (linear predictor – 2.52). The probability of surviving to any time up to 2 years, from the decision point, can then be readily calculated from the Weibull survival function with a shape parameter of 0.637.

Table 19 illustrates the predicted outcomes for several BASIL trial patients from across the range of prognostic scores.

Nature and timing of interventions after randomisation

A total of 228 patients were randomised to bypass surgery and 224 to balloon angioplasty. The assigned intervention was attempted during the first year after randomisation in 85% and 96% of those allocated to bypass surgery and balloon angioplasty respectively (CONSORT diagrams showing patient flows into and through the trial are presented in Chapters 2 and 3).

However, some of those interventions were delayed, and the rate of early secondary procedures was also quite high. All interventions undertaken at any time during follow-up (range 3–7 years), including repeat procedures and those carried out as secondary procedures at the same time as the primary procedure, are shown in Table 21.

The cumulative number of treatments received by patients over the first 12 weeks from randomisation is shown in Table 22.

By 12 weeks after randomisation nine (4%) balloon angioplasty patients versus 23 (10%) bypass surgery patients had not undergone revascularisation; three (1.3%) balloon angioplasty versus 13 (5.8%) bypass surgery patients had undergone the opposite treatment first; and 35 (15.6%) balloon angioplasty and two (0.9%) bypass surgery patients had received the assigned treatment and then undergone the opposite treatment for immediate technical or early clinical failure. Overall, 21 patients underwent more than two attempts at revascularisation during the first 12 weeks after randomisation. However, the rate of new interventions levels off by week 8 after randomisation. We have, therefore, chosen to analyse outcomes according to the interventions received during the first 8 weeks following randomisation. The reasons for no intervention being carried out during the first 8 weeks after randomisation in patients assigned to angioplasty or surgery are shown in Table 23. Table 24 provides further details of all first and subsequent attempts at revascularisation during the first 8 weeks after randomisation by randomised group; the short-term outcome of those attempted revascularisations and the patients’ status (amputation, death) at 8 weeks.

Surgery was attempted as a first revascularisation procedure within 8 weeks of randomisation in 185 patients. In 171 patients bypass surgery was immediately technically successful and no further attempt at revascularisation was undertaken during the 8 weeks after randomisation or within 30 days (whichever was the longest). However, by 8 weeks, 12 of these 171 patients were dead and four had undergone major amputation of the trial (operated) leg. In three patients, bypass surgery was judged an immediate technical failure; one patient went on to have no further revascularisation during the 8 weeks after randomisation or within 30 days and two patients went on to have further surgery during this time period; one of these went on to amputation within the 8-week/30-day period. Eight patients had bypass surgery as a first revascularisation that was judged to be an immediate technical success but went on to have balloon angioplasty (seven patients) or further surgery (one patient) during the 8 weeks after randomisation or within 30 days. Two patients had bypass surgery combined with balloon angioplasty as a technically successful first and only revascularisation during the first 8 weeks.

Procedures and outcomes in the 224 patients who underwent balloon angioplasty as the first attempted revascularisation during the first 8 weeks can be found in Table 24 in the same way. Overall, in the first 8 weeks after randomisation, patients randomised to balloon angioplasty were more likely to have their assigned treatment first (208/224, 93% versus 182/228, 80%, p = 0.01, chi-squared test) while those randomised to bypass surgery were more likely to have the opposite treatment first (16/228, 7.0% versus 3/224, 1.3%, p = 0.04, Fisher’s test) or no revascularisation (30/228, 13.1% versus 13/224, 5.8%, p = 0.01, Fisher’s test).

The number of patients assigned to balloon angioplasty who did not receive their randomised allocation as the first treatment was too small to make comparisons with those that did. However, those that were assigned to bypass surgery and who did and did not receive surgery as their first treatment were not different in terms of five baseline characteristics (age, below-knee Bollinger angiogram score, presence of tissue loss, serum creatinine, numbers of ankle pressures obtainable) that best predict the subsequent OS of the BASIL trial cohort as a whole (see Chapter 4).

Patients who had balloon angioplasty as their first attempted revascularisation within the first 8 weeks were more likely to suffer an immediate technical failure (as judged by the responsible interventionalist at the time) or early clinical failure (requirement for further revascularisation procedure within 8 weeks after randomisation or 30 days whichever was the longest) (60/224, 27%) than those who had bypass surgery as a first completed revascularisation procedure during the first 8 weeks after randomisation (14/185, 7.0%, p < 0.001, chi-squared test). In 42/60 (70%) patients, a failed first attempt at balloon angioplasty was followed by a further intervention and in 39/42 (93%) cases that was surgery (37 bypass surgery).

Those patients who had successful and unsuccessful first attempted balloon angioplasty could not be distinguished by the predictive baseline characteristics (see Chapter 4).

Immediate outcomes by treatment received

Those who had angioplasty as their first intervention were more likely to suffer a primary or secondary failure (60/222, 27%) than those who had surgery as a first procedure (11/184, 6.0%, p < 0.001, chi-squared test) (Table 24).

In 42/60 (70%) patients, failed angioplasty was followed by a further intervention and in 36/42 (86%) cases this was bypass surgery. Those patients who had successful and those who had unsuccessful angioplasty could not be distinguished by the predictive baseline characteristics; in particular, the below-knee Bollinger angiogram scores and the number of ankle pressures measurable had a similar distribution in the two groups (Table 27).

Subsequent outcomes by treatment received

For the reasons set out above, to describe subsequent outcomes by treatment received we have chosen to divide the BASIL patient cohort into five groups based upon the nature of the interventions performed during the first 8 weeks after randomisation; namely:

• group 1: successful surgery only in first 8 weeks (n = 173)

• group 2: successful angioplasty only in first 8 weeks (n = 162)

• group 3: unsuccessful surgery (technical failure or further intervention within 8 weeks) (n = 11)

• group 4: unsuccessful angioplasty (technical failure or further intervention within 8 weeks) (n = 60)

• group 5: no intervention in first 8 weeks (n = 46).

For group 1 we have further considered outcomes by whether vein (group 1a, n = 132) or prosthetic material (group 1b, n = 41) was used as the conduit.

For group 2 we have further considered outcomes by whether the transluminal (group 2a, n = 87) or subintimal (group 2b, n = 75) route was used (as recorded at the time by the responsible interventionalist).

Balloon angioplasty groups (2 and 4)

Describing often complex attempts at balloon angioplasty for severe multilevel disease is more difficult than describing bypass surgery. We have chosen to describe the balloon angioplasty in groups 2 and 4 by number of disease lengths treated (a disease length may extend across several anatomic arterial segments) and the number of anatomic arterial segments treated. With regard to the former, although in the majority of patients (159/224, 72%) interventionalists reported that they had attempted to treat a single length of disease, in a substantial number of patients it was reported that attempts had been made to treat more than one (up to four) separate disease lengths (Table 29). The numbers of reported transluminal (n = 92) and subintimal (n = 105) balloon angioplasty procedures were approximately equal with just over 10% being reported as mixed. The pattern and extent of anatomic segments treated was also complex (Table 30). As expected, the majority of patients underwent treatment of the superficial femoral artery (n = 177) either alone (n = 68) or in combination with the popliteal artery (n = 74) and crural arteries (n = 35). Most of the remaining patients underwent treatment of the popliteal segments either alone or more usually in combination with crural arteries; the number of isolated crural artery balloon angioplasties was small. Despite the larger number of unsuccessful balloon angioplasties, as with the surgery groups, it does not appear possible to distinguish successful and unsuccessful procedures in terms of the numbers of disease lengths treated, the type of balloon angioplasty or the anatomic segments treated. Table 31 shows the subsequent treatments undertaken by the patients with failed primary procedures (groups 3 and 4).

TABLE 29 - Number of disease lengths treated and type of balloon angioplasty in 222 patients undergoing attempted balloon angioplasty as their first attempted revascularisation in the first 8 weeks after randomisation (treatment groups 2 and 4)

Unsuccessful balloon angioplasty indicates immediate technical failure or further intervention within 8 weeks of randomisation or 30 days, whichever was longer.

	Group 2: Successful angioplasty only (n = 162)	Group 4: Unsuccessful angioplastya (n = 60)
Number of disease lengths treated
1	115 (71%)	44 (73%)
2	26 (16%)	14 (24%)
3	19 (12%)	2 (3%)
4	2 (1%)	–
Type of balloon angioplasty attempted
Transluminal	70 (43%)	22 (37%)
Subintimal	74 (46%)	31 (52%)
Mixed	18 (11%)	7 (11%)

TABLE 30 - Anatomic segments treated in 222 patients undergoing attempted balloon angioplasty as their first attempted revascularisation in the first 8 weeks after randomisation (treatment groups 2 and 4)

AKPA, above-knee popliteal artery; ATA, anterior tibial artery; BKPA, below-knee popliteal artery; CA, crural artery; PerA, peroneal artery; PTA, posterior tibial artery; SFA,superficial femoral artery.

Anatomic segments treated	Group 2: Successful angioplasty (n = 162)	Group 4: Unsuccessful angioplasty (n = 60)	Total
SFA ± distal segments
SFA only	49	19	68
SFA + AKPA	44	14	58
SFA + AKPA + BKPA	14	2	16
SFA + AKPA + BKPA+ trifurcation	1	2	3
SFA + AKPA + BKPA + CA unspecified	12	3	15
SFA + AKPA + BKPA+ PerA	0	3	3
SFA + AKPA + BKPA + ATA + PTA	9	3	12
SFA + AKPA + BKPA + ATA + PTA + PerA	1	1	2
Subtotal	130 (80%)	47 (78%)	177
AKPA ± distal segments
AKPA only	10	5	15
AKPA + BKPA	4	2	6
AKPA + BKPA + CA unspecified	2	1	3
AKPA + BKPA + ATA + PTA	3	0	3
AKPA + BKPA + PerA	1	0	1
AKPA + BKPA + ATA + PTA + PerA	2	0	2
Subtotal	22 (14%)	8 (14%)	30
BKPA ± distal segments
BKPA only	1	2	3
BKPA + trifurcation	2	0	2
BKPA + CA unspecified	5	3	8
Subtotal	8 (5%)	5 (8%)	13
Crural arteries only
PerA only	1	0	1
ATA + PTA	1	0	1
Subtotal	2 (1%)	0 (0%)	2
Total	162	60	222

TABLE 31 - Further treatments after a failed primary procedure (groups 3 and 4) within the first 8 weeks from randomisation or 30 days after the primary intervention

BAP, balloon angioplasty; BSX, bypass surgery.

Next treatment	Group 3: Unsuccessful bypass surgery (n = 10)	Group 4: Unsuccessful balloon angioplasty (n = 60)	Total
No further treatment	1	12	13
BSX and endarterectomy	0	1	1
BSX	2	37	39
Endarterectomy	0	1	1
BAP	1	7	8
Stent	1	0	1
Chemical sympathectomy	0	1	1
Thromboembolectomy	6	1	7
Total	11	60	71

Survival curves for these five groups are shown in Figure 15. AFS (p = 0.003, log rank test) but not OS is significantly worse in those patients who have a failed angioplasty (group 4) compared with those having an initially successful (group 2) angioplasty. Neither AFS nor OS is significantly worse after failed surgery (group 3 versus group 1); however, with only 11 failed cases, this comparison has very low power. There are few differences between the other groups and none are significant. Those with no interventions in the first 8 weeks have slightly poorer AFS and OS initially but their long-term survival is somewhat better than the groups treated successfully.

FIGURE 15.

(a) Amputation-free survival and (b) overall survival curves for the five by-treatment groups.

Vein versus prosthetic bypass surgery

For group 1 we further considered outcomes by whether vein (group 1a, n = 127) or prosthetic material (group 1b, n = 42) was used as the conduit for bypass surgery. Patients receiving successful vein bypass as their first and only treatment in the first 8 weeks after randomisation (group 1a) had a better outcome in terms of AFS (p = 0.003, log-rank test).but not OS (p = 0.38, log-rank tests) than those receiving successful prosthetic bypasses as their first and only treatment in the first 8 weeks (group 1b) (Figure 16). There was no significant association between the use of prosthetic material for bypass and any of the baseline clinical data (see Chapter 4).

FIGURE 16.

(a) Amputation-free survival and (b) overall survival curves for patients undergoing initially successful surgery (group 1) according to type of bypass conduit.

Subintimal versus transluminal balloon angioplasty

For group 2 we have further considered outcomes by whether the transluminal (group 2a, n = 87) or subintimal (group 2b, n = 75) route was used for the first segment treated (as recorded at the time by the responsible interventionalist) for balloon angioplasty. There were no differences in terms of AFS and OS, respectively, between transluminal and subintimal angioplasty (Figure 17).

FIGURE 17.

(a) Amputation-free survival and (b) overall survival curves for patients undergoing initially successful angioplasty (group 2) by type (transluminal versus subintimal).

Outcomes of bypass after failed angioplasty

The 37 patients in group 4 who underwent bypass surgery after first attempted failed angioplasty had a poorer AFS (p = 0.006, log rank test) and a somewhat poorer OS (p = 0.06, log rank test) than the 184 patients in groups 1 and 3 who underwent bypass surgery as their first treatment (Figure 18).

FIGURE 18.

(a) Amputation-free survival and (b) overall survival in patients randomised to and undergoing bypass surgery and patients undergoing bypass surgery after failed angioplasty.

Summary of scores by segment

The distribution of disease at each arterial segment is given in Table 33 and shown graphically, without the plantar arch data, in Figure 20. We can see that the greatest burden of disease is in the tibial arteries and in the segments above the knee.

FIGURE 20.

Distribution of Bollinger scores (0 to 15) in each arterial segment (plantar arch excluded). The proportions of each segment occluded are shown with the heaviest shading at the bottom of each bar, partially affected segments have intermediate shading and the proportions unaffected in each bar are shown ‘unshaded’ at the top of each bar. PFA, profunda femoris; Pr-SFA, Di-SFA, proximal and distal superficial femoral; Pr-PA, Di-PA, proximal (above-knee) and distal (below-knee) popliteal; TPT, tibioperoneal trunk; Pr-PT, Di-PT, proximal (upper half calf) and distal (lower half calf) posterior tibial; Pr-AT, Di-AT, proximal and distal anterior tibial; Pr-Per, Di-Per, proximal and distal peroneal.

Table 34 shows the number of sites scored per patient, excluding the plantar arch. Very few patients have anything other than complete data. The mean score was therefore computed by taking the mean of all available data for each patient, equivalent to imputing the missing values by the mean of the other segments for this patient.

Comparison of disease in the two treatment arms

Mean scores for the above-knee and below-knee segments, and for each individual segment (excluding the plantar arch) by randomised group are shown in Table 35. As to be expected from the randomisation process, the two groups were very well matched on individual segment and overall mean scores. All further analysis is therefore presented for the trial cohort as a whole.

Analysis of patterns of disease in the trial cohort as a whole

Exploratory analyses were carried out to further understand the pattern of disease in these patients. The data were divided into five approximately equal-sized groups (83, 87, 84, 80, 84 – uneven numbers due to ties) according to their mean overall score from 1 (best) to 5 (worst). Figure 21 shows the mean score at each of the segments for the five groups.

We can see that all the groups have disease in the upper segments, while the lower segments are progressively more affected in those groups with higher mean scores. The central segments only become affected in the most severe groups. Patients with the least overall disease tend to have their disease concentrated in the SFA and popliteal artery which were the commonest sites of disease overall. As the overall severity of disease increases, the crural arteries become increasingly involved in addition to the more proximal disease. The posterior tibial was the worst affected crural artery while the peroneal appears relatively spared.

FIGURE 21.

Pattern of disease in five approximately equal-sized groups according to mean overall Bollinger score, where group 1 is least overall disease and group 5 is worst overall disease. Profunda femoris (PFA); proximal and distal superficial femoral (Pr-SFA, Di-SFA); proximal (above-knee) and distal (below-knee) popliteal (Pr-PA, Di-PA); tibioperoneal trunk (TPT); proximal (upper half calf) and distal (lower half calf) posterior tibial (Pr-PT, Di-PT); proximal and distal anterior tibial (Pr-AT, Di-AT); proximal and distal peroneal (Pr-Per, Di-Per).

Correlations between disease burdens in the 13 different arterial segments are shown in Table 36.

The strongest relationships are between disease in the:

• proximal and distal SFA

• distal popliteal and tibioperoneal trunk

• tibioperoneal trunk and proximal PT and peroneal

• proximal and distal halves of the three crural vessels (PT, AT, peroneal).

There are also some interesting negative correlations. Specifically, it appears that significant disease is often present in the SFA or the popliteal/TPT segment but not both. This probably reflects the fact that to be randomised in BASIL the patients had to be treatable by both surgery and angioplasty. Patients with very extensive disease would have been untreatable or only treatable by bypass.

It therefore appears that to be considered treatable by angioplasty, interventional radiologists required most of the BASIL patients randomised to have a re-entry point, usually around the level of the knee. This is further shown in Tables 37 and 38.

Above-knee and below-knee Bollinger scores and outcomes

These exploratory analyses suggest that, in the analysis of the outcomes of the trial we should consider separately the mean Bollinger scores for arterial segments above and below the knee (excluding the plantar arch). The contribution these mean scores make to predicting outcome is presented in Chapter 4.

Relationship between Bollinger score and TASC II scores

TASC II scores were available for 411 of the 418 patients with Bollinger scoring. The relationship between increasing burden of disease on Bollinger scoring, TASC II score and BASIL stratification group at randomisation (see Chapter 2) is shown in Table 39. As expected, trial patients are predominantly in the higher TASC II groups, with very few in group A.

Although the TASC II and Bollinger scores are generally related, there are also many cases where they disagree. Furthermore, there is very little evidence of a relationship between the TASC II score and clinical presentation. In Chapter 4 we show that the Bollinger scores, especially the lower leg mean score, are much more strongly related to the outcomes than is TASC II classification.

Bollinger scores do not relate closely to BASIL trial stratification group either (Table 40).

Overview

The BASIL trial design integrated measurement of survival, AFS, HRQoL and the use of hospital inpatient services. These trial outcomes allowed consideration of the primary health and resource consequences following different strategies for managing SLI. Individual patient hospital costs were collected to the end of follow-up. All analyses were by intention to treat using the perspective of the individual patient for HRQoL and the hospital sector for resource use.

Health-related quality of life

We measured HRQoL using standard generic and disease-specific measures. Two generic measures, the EQ-5D42 and the SF-36,43 were used along with the VascuQoL. 53 For EQ-5D, SF-36 scales/summary scores and VascuQoL, higher scores indicate better health and well-being as perceived by the patient.

These measures were collected using a self-administered protocol at baseline/randomisation and at 3, 6, 12, 24 and 36 months after randomisation. All patients were asked to provide HRQoL data out to 3 years from randomisation whether or not they had undergone major amputation of the trial leg. The HRQoL questionnaires are shown in Appendix 4.

EuroQoL 5D

The EQ-5Dindex covers five dimensions: mobility, self-care, usual activity, pain/discomfort and anxiety/depression. Each dimension has three levels (no problem, some problem or extreme problem) and subjects are asked to indicate the level that corresponds to their current level of function or experience on each dimension.

The EQ-5D responses were converted into a single weighted utility (preference-based) score using the original time trade-off tariff set. 44 This is a standard and well-established set of preference weights used in clinical and economic evaluations based on experimental, observational and modelling studies using UK populations. Overall self-rated health status was also collected using the EQ-5Dvas visual analogue score (0 equals worst health and 100 equals best health).

Short Form 36

The SF-36 contains 36 items/questions that measure HRQoL across eight domains: physical functioning, social functioning, role limitations due to physical problems, role limitations due to emotional problems, mental health (general mood or affect including anxiety, depression and psychological well-being), energy/vitality, bodily pain and general health perceptions. For each dimension, question responses were coded, scored and transformed into a scale from 0 (worst possible score) to 100 (best possible score). The SF-36 items were combined into physical and mental component summary scores using recommended procedures. 45

The Short Form 6D (SF-6D), a single index preference-based measure, was also derived from the SF-36 responses using the Brazier algorithm. 59 This provided a further summary measure of the SF-36 items using a health-state valuation model that complements the EQ-5D. As it is based on the broader and more detailed SF-36 items, and has a strong theoretical and methodological basis, the SF-6D enabled us to consider whether the level of and change in patients’ perception of their well-being following randomisation was similar across these two leading preference-based measures of well-being.

Vascular Quality of Life Questionnaire

The VascuQoL is a disease-specific questionnaire designed to assess specific elements of HRQoL for individuals with lower limb ischaemia. It includes 25 items (questions) subdivided into five domains: pain (four questions), symptoms (four questions), activities (eight questions), social (two questions) and emotional (seven questions). Each question has a seven-point response scale ranging from 1 (worst possible) to 7 (best possible). Responses were averaged for individual domain and composite total scores giving equal weight to each question and domain.

Missing values

We report analyses using available data for all HRQoL end points (case-wise deletion of observations when HRQoL scores were missing). We expected that attrition over time would occur as the horizon for follow-up increased and that missing scores would become more prevalent as trial participants dropped out or failed to complete/return questionnaires. Disregarding observations with missing scores wastes data, reduces power and possibly produces biased estimates of key parameters like the EQ-5D. We therefore employed an imputation method for missing values using all available information following multivariate imputation by chained equations60,61 for missing EQ-5Dindex scores that were used in the QALY analysis. We chose this multiple imputation approach because it has attractive theoretical and methodological properties and is a more powerful and flexible tool when the level of missingness is around 10–60%.

The multivariate imputation model assumes that missing data are missing at random, i.e. that a value being missing may depend on the observed data but not the unobserved data and that the observed data can be used to generate information about the missing values. The multivariate imputations were generated by applying sequential linear regressions, where each incomplete variable was imputed conditionally on all variables in an iterative way. The procedure for selecting variables for predicting missing values was based on using variables with the highest bivarate correlations with the variable being predicted. Redundant variables that added little to the predictions were dropped as were highly collinear variables. We estimated missing values for each of the six EQ-5D scores (baseline, 3, 6 12, 24 and 36 months) using the other five EQ-5D scores, the natural log of survival times and gender. Age and survival status at 3 years were considered but were eliminated from the final prediction equations. We did not include any other variables that could predict missingness in the model. We chose a relatively high number of imputations (10) to increase the efficiency of estimates given the high rate of missingness in the EQ-5D scores. The results were then pooled across the imputed complete data sets using average values for EQ-5D scores.

The QALYs were calculated on an individual patient basis using the EQ-5Dindex. Specifically, a standard multiplicative model was used to estimate QALYs by the area under linear interpolation of the EQ-5Dindex trajectory for each individual using the intervals in months [0, 3], [3, 6], [6, 12], [12, 24] and [24, 36]. These utility-adjusted survival time intervals were summed to generate a total QALY score for each patient. Although, as described in Chapter 3, we did measure survival beyond 3 years (all patients were followed for a minimum of 3 years and 54% for 5 years) and did collect some HRQoL data for a longer time, we chose not to estimate QALYs beyond 3 years from randomisation because of the incomplete clinical follow-up coupled with an increase in the proportion of HRQoL non-responders.

Inpatient hospital use and cost

Resource-use data were collected following randomisation on the index intervention and all subsequent interventions, hospital stays and hospital clinic visits (see data capture forms in Appendix 3). Patient-specific hospital use was measured using the overall duration of stay for each hospital inpatient episode and the number of day-patient/outpatient visits. Acute hospital inpatient days were disaggregated by surgical and medical specialty (e.g. vascular surgery, HDU, ITU, cardiology, general medicine, rehabilitation) based on the reasons for admission and recorded interventions/procedures. Hospital activity data were recorded in all of the participating centres on an individual patient basis. Cumulative hospital episodes, days and visits were restricted to 1, 3 and 7 years from the date of randomisation. These measures of hospital resource use were converted into cost estimates using NHS hospital costs derived routinely for Scotland – a region of the UK that accounted for 31% (142/452) of randomised patients in the trial. The inpatient days, broken down by specialty, were valued using the average specialty-specific cost per day obtained from the Scottish system of hospital cost statistics. 54 Day-patient/outpatient visits were costed on a per diem/attendance basis.

All procedure costs (surgical, radiological and amputations) were measured using patient-specific anaesthetic, theatre and recovery suite timings, the number and grades of medical, nursing and theatre staff and the specific procedure-related equipment and consumables.

Data capture forms in Appendix 3 show the details of what was recorded. Staff time was valued using UK national pay scales. Purchase costs were used to value the typical mix of equipment and consumables used in the surgical and radiological procedures.

Hospital-use and procedure costs were calculated on a price base of the financial year 2006–7 in UK pounds sterling. A discount rate of 3.5% recommended by HM Treasury was used to calculate the present value of annual costs incurred over 3-year and 7-year time horizons from the date of randomisation. We discounted health effects at 3.5% following current guidance from the National Institute for Health and Clinical Excellence (NICE) suggesting that both costs and health effects should be discounted using a uniform rate. We also estimated undiscounted health effects as arguments continue about the theoretical rationale and methodological implications of differential discounting of costs and effects in economic evaluations of health programmes.

Analysis of HRQoL and hospital costs

Descriptive statistics were based on baseline and follow-up HRQoL questionnaires for cases with no missing items (fewer than 1% of completed questionnaires had missing items). Unadjusted differences in mean EQ-5D weighted scores, SF-36 component summary scores and VascuQoL total scores were assessed using simple linear regressions. Adjusted differences allowing for baseline scores were based on a nearest-neighbour matching estimator. 46 As simple matching estimators are biased when the matching is not exact, a bias-corrected matching estimator was used which adjusts the difference within the matches for the differences in their covariate values.

Arithmetic mean and median costs based on all patients were calculated using the full sample method with no allowance for right censored cases. Given the complete follow-up to at least 3 years for all cases, censoring would have no effect on costs truncated at this point. The impact of right censored cases for longer follow-up is unclear as standard life-table methods may generate bias in estimates of mean costs (and mean survival and quality-adjusted survival times) when informative censoring is present (i.e. patients may incur higher costs in close proximity to death).

Confidence intervals for estimated untransformed arithmetic mean costs were estimated analytically and empirically using bootstrapping techniques to check for the adequacy of the assumptions made regarding the normality of the cost distributions. We found that standard t tests and t test-based confidence intervals were very similar to those based on the bootstrap. We did not allow for any arbitrary differences in the cost per inpatient day or the cost of treatment for specific interventions (e.g. radiological or surgical procedures) using deterministic sensitivity analyses as we felt that the stochastic uncertainty around our cost estimates would easily encompass such assumptions. For example, increasing/decreasing the cost of hospital treatment by an arbitrary 10% for interventions where we might expect service use to be more/less resource-intensive across the 26 centres would in any case have little material impact on the confidence intervals surrounding the point estimate of the difference in average total costs. Extreme value analysis of single (or multiple) resource parameters was not conducted nor did we try to calculate threshold values leading to a convergence or even reversal of the cost estimates that we present for each trial arm.

Cost-effectiveness measures

Incremental cost-effectiveness ratios were estimated using the mean difference in hospital costs and the mean difference in effectiveness between the angioplasty and surgery groups. We considered a range of effectiveness measures using mean differences in AFS (the primary end point of the trial) in days, mean differences in OS and patient-specific total QALYs to 36 months based on the EQ-5D. To capture the uncertainty surrounding the estimate of mean differences in costs and effects we used both analytical and non-parametric bootstrap methods. We report the joint distribution of differences in costs and effects using analytical methods based on a bivariate normal distribution allowing for covariance between mean cost and effect differences. Visual presentations of cost-effectiveness are reported using confidence ellipses (50%, 90% and 95%) to capture the magnitude and precision of differences in costs and effects. Scatterplots of incremental costs and effects and corresponding confidence ellipses based on a non-parametric bootstrap technique were also calculated using 5000 resamples of the difference in cost and effects drawn with replacement from the original sample of patients. We also summarise our cost-effectiveness results within a net benefit approach using incremental net (monetary) benefit and cost-effectiveness acceptability curves. Net benefit in this framework is defined as the monetary equivalent of the incremental health effects less incremental costs. The monetary equivalent of the health effects is the product of decision-makers’ willingness to pay (WTP) for a one unit gain in health benefit (e.g. £30,000 per QALY) and the health benefit (e.g. amputation-free life-year, life-year or QALY gained). As the WTP value per unit of health benefit is generally unknown or will vary between decision-makers, the estimated net monetary benefit is calculated and plotted for different values of WTP. The standard interpretation is that a treatment is cost-effective if the net monetary benefit is greater than zero. When the joint distribution is (roughly) centred on zero, there may be no monetary values attached to the health outcome where a reasonable percentage of the joint distribution is cost-effective/cost-ineffective. We addressed this possibility by estimating cost-effectiveness acceptability curves that present the probability that the alternative is cost-effective (the net monetary benefit is positive) allowing for different ceiling values for a decision-maker’s WTP per unit of health benefit.

All health economic analyses were conducted using Stata Statistical Software, release 10. Imputations for missing EQ-5Dindex scores were generated using an algorithm for creating models for imputation (Stata packages pred_eq and check_eq and the Stata ice package). 62

SF-36 health dimensions and summary scores

The SF-36 domains and summary scores [based on 213/224 (95%) responders in the angioplasty group and 207/228 (91%) responders in the surgery group with complete questionnaires] were similar in the two trial arms at baseline (before randomisation) although those subsequently randomised to bypass surgery appeared to have very marginally, probably clinically insignificantly, better HRQoL (Table 41).

The distributions were generally positively skewed with evidence of moderate positive kurtosis, reflecting relatively peaked distributions. At baseline, BASIL patients perceived their health to be much lower than that reported in general populations (matched for age and gender) and patients undergoing endovascular or conventional aortic aneurysm repair. 63 Large floor effects (proportion of patients in the worst possible health states) were observed for the role physical (82%) and role emotional (61%) scales. With the exception of role emotional (29%), ceiling effects (proportion of patients in the best possible heath state) were small and well below 10% for most scales.

Patients in both treatment groups reported improved SF-36 scales and summary scores by 3 months (Table 42), but little improvement was recorded beyond 3 months. Most of the gains in SF-36 are concentrated in the scales which capture perceptions of physical well-being. However, there is also a very large increase in the emotional dimension of the SF-36 and there is some slight improvement over a longer time period in the SF-36 mental health domain.

Vascular Quality of Life Questionnaire

The disease-specific VascuQoL scales provide further evidence that both angioplasty and surgery have a positive impact on all domains affected by SLI (Table 43). 64 As with the SF-36, the VascuQoL domains all record higher scores (better HRQoL) at baseline in those that are subsequently randomised to surgery. This is maintained and, in fact, disease-specific HRQoL is better in those randomised to surgery in every domain and at every time point out to 24 months. Interestingly, at 36 months, this reverses and angioplasty appears to be associated with superior HRQoL (Figure 22).

FIGURE 22.

Unadjusted mean VascuQoL total scores by trial arm at baseline (before randomisation) and various time points thereafter.

The question is whether surgery affords some advantage over angioplasty in terms of generic and, perhaps more relevantly, disease-specific HRQoL at least in the short term (12–24 months). Unadjusted mean VascuQoL total scores by trial arm at baseline (before randomisation) and various time points thereafter are shown in Figure 22. Overall, these data suggest that any advantage to surgery may be largely due to the surgery group having a slightly better HRQoL at baseline rather due to any additional benefit from bypass surgery over balloon angioplasty in terms of HRQoL.

EuroQoL and SF-6D

This general pattern of improvement is also reflected in the EuroQoL and SF-6D weighted index scores (Table 44).

Summary

Although there is some weak evidence that HRQoL may be somewhat better in the bypass surgery group, there are no significant differences in HRQoL when the two treatment groups are compared; especially when post-randomisation scores are adjusted for differences in scores at baseline (before randomisation). Furthermore, the HRQoL from surviving responders is likely to be substantially better than that for the trial cohort as a whole and in each trial arm separately.

Crude and adjusted differences in SF-36 (Table 45), VascuQoL (Table 46), EQ-5D and SF-6D (Table 47) scores are very similar and not significantly different from zero at all time intervals up to 36 months. Patients in both treatment groups reported virtually identical levels and trajectories in the EQ-5D and SF-6D over time.

Imputation of missing values

As might have been expected, HRQoL response rates fell significantly over time. Data for the EQ-5D, used to undertake the cost per QALY analysis, are shown in Table 48; response data for the other HRQoL instruments were very similar. In other words, individual patient response rates were similar across all the questionnaires that they were asked to complete. Response rates in the two arms were very similar.

Although all patients known to still be alive were asked to complete the HRQoL questionnaires, perhaps not surprisingly, those patients who had already undergone major limb amputation were less likely to respond. It may also be reasonable to presume that those with the lowest HRQoL, many of whom were under continuing hospital care for their SLI and a range of other comorbidities, were less likely to return their questionnaires. So it may be that the data restricted to complete cases only present an overoptimistic picture of the results of the intervention; in other words, those patients who are doing well (after both balloon angioplasty and bypass surgery) may be substantially over-represented among the responders.

Without the multiple imputations and using only complete data, we would have only been able to analyse a very small number of cases. We considered it more sensible to use all of the available information, conduct the multiple imputations using appropriate methods and then analyse the distribution of EQ-5D scores using complete data based on actual and imputed values.

Table 49 provides imputed and recorded mean EQ-5D scores at time intervals up to 3 years following randomisation. The complete data imputed for patients who were alive and could have returned questionnaires is also presented for individuals by amputation status. There is very little difference between the mean scores calculated for recorded data and imputed data at baseline and early periods following randomisation (< 12 months) where the degree of ‘missingness’ is relatively low. As the response rates deteriorated over time, the scores based on complete imputed data are lower than those based solely on the complete recorded data. A widening gap also emerged between the imputed scores for survivors with or without an amputation. The individuals without an amputation appeared to fare better with higher EQ-5D scores compared with survivors with an amputation who could have completed this measure of self-reported well-being. Table 50 compares the treatment groups using the imputed EQ-5D scores. There is a small but persistent advantage in favour of surgery when the EQ-5D is assessed at all time intervals up to 3 years. These data are summarised graphically in Figure 23.

FIGURE 23.

Imputed EQ-5D mean scores (n) by treatment group from baseline to 36 months follow-up showing effect of amputation and of randomised treatment.

Hospital admissions and length of stay

The use of inpatient hospital services over time was broadly similar for patients in both trial arms as measured by the number of hospital admissions and total days spent in hospital (Table 51). Over the first year from randomisation, patients in the surgery group were in hospital for about a week longer than those in the angioplasty group. The difference in hospital stay shifted in favour of surgery over the longer run as the angioplasty patients used slightly more inpatient care over the medium to long run. Over a 7-year time horizon the average number of hospital stays for both groups was four and average length of stay, averaged over all inpatient admissions, was just over 2 months (71 days). It is striking, therefore, that on average, these patients spent the best part of 5–6 weeks of their first post-randomisation year in hospital; then 2–3 weeks per year thereafter. It is worth noting that these data reflect only acute hospital resource use and exclude time spent, for example, in ‘step-down’ facilities for rehabilitation after amputation.

Given the additional short-term morbidity of surgery (see Chapter 2), there is less of a difference between the two trial arms than might perhaps have been expected. However, these data probably reflect the fact that there is a range of (medical and social) factors, other than the status of the trial leg and its treatment, that determine admission, readmission and length of stay in hospital, and patients randomised to angioplasty have a significantly higher immediate failure and reintervention rate (see Chapter 2).

Patients’ inpatient episodes primarily occurred in ward settings with very little use of the more specialised services provided in HDU and ITU (Table 52). Patients randomised to a surgery-first strategy used around a half day more of HDU on average compared with angioplasty-first patients. There is a slight difference in ITU use with a few additional hours used by the surgery-first patients. The main cost driver remains the number and duration of episodes in acute ward settings.

Table 53 presents more detail on the structure of costs incurred in the hospital wards and theatres. After 3 years of follow-up, theatre costs account for 9% of total hospital costs in the angioplasty-first group. As expected, the corresponding figure is higher at 14% for the surgery-first group. Most of the theatre and hospital ward costs fall in the first year following randomisation.

Hospital costs

Over the first year from randomisation the mean cost of inpatient hospital treatment in patients randomised to surgery was estimated as £22,002 (£18,369 hospital stay and £3635 procedure costs), which is approximately a third higher than the £16,582 (£14,468 hospital stay and £2115 procedure costs) for patients randomised to angioplasty (see Chapter 2) (Table 54). This difference in mean total hospital and procedure costs of around £5420 was significant (95% CI £1547 to £9294) at 1 year. However, because of increased costs incurred by the angioplasty patients in subsequent years, at the end of 7 years this difference decreased to £2310 (£33,539 surgery vs £31,228 angioplasty) and was no longer significant (see Chapter 3). The median cost of inpatient hospital treatment showed a slightly different pattern, with significant differences emerging in favour of angioplasty (i.e. lower median costs) for the first year following randomisation and for cumulative costs up to 7 years (£24,959 surgery versus £18,256 angioplasty).

Point estimates of cost-effectiveness

Point estimates of cost-effectiveness can be calculated by comparing average differences in hospital costs and average differences in treatment effects; in this case AFS and OS at different points in time after randomisation.

Seven-year (non-quality-adjusted) analysis

If we first take a 7-year perspective on (non-quality-adjusted) AFS and hospital costs those patients randomised to surgery are estimated to live, on average, 32 days longer with their trial leg intact at an estimated additional average hospital cost of £2310 when compared with those randomised to angioplasty. The additional cost per AFS year is £26,032 [(£2310/(32.4/365.25)]. Similarly, when the estimated additional hospital cost of surgery out to 7 years (£2310) is compared with the additional estimated average gain in OS (20 days) the cost-effectiveness ratio is £41,401 [£2310/(20.4/365.25)].

Three-year (quality-adjusted) analysis

Taking a three-year perspective, using the available baseline to 36 months HRQoL (imputed EQ-5D) data to perform a quality-adjusted life analysis we find that patients randomised to surgery are estimated to enjoy, on average, an additional 10 quality-adjusted life days at an estimated additional average hospital cost of £3533 when compared with those randomised to angioplasty. This point estimate of the cost-effectiveness over 3 years generates a ‘cost per QALY’ of £134,257 [£3533/(9.6/365.25)].

Relationship between differences in cost and differences in amputation-free survival

The relationship between bootstrapped estimates of the difference in cost (surgery less angioplasty) between the two trial arms and the differences in amputation-free life-years (surgery less angioplasty) out to 7 years is shown in Figure 24. The interpretation of each quadrant is:

• upper right: surgery more costly with additional AFS days

• lower right: surgery less costly with additional AFS days

• upper left: surgery more costly with fewer AFS days

• lower left: surgery less costly with fewer AFS days.

FIGURE 24.

Incremental costs and incremental amputation-free life-years calculated over 7 years (surgery versus angioplasty bootstrapped estimates).

About half of the distribution (50.2%) is located in the upper right quadrant of the graph (more costly and more effective) but it also extends well into the lower left quadrant (more expensive, fewer amputation-free life-years). A further 26.4% is located in the upper left quadrant (more costly and less effective) with 17.8% in the lower right quadrant (less costly and more effective) and 5.6% in the lower left quadrant (less costly and less effective).

Along with this empirical distribution broken down into the quadrants, we also report confidence ellipses (50%, 75% and 95%) surrounding the point estimate of cost-effectiveness to describe the distribution of incremental costs and effects (Figure 25). These data can, therefore, be used to create a cost-effectiveness acceptability curve,66 which shows the probability that a surgery-first strategy is cost-effective, assuming different ceiling levels for the value placed on an amputation-free life-year (Figure 25). At a WTP value of £26,032 the probability is equal to 0.5 by construction as this is the point estimate of the cost-effectiveness ratio. The curve is relatively flat beyond this point suggesting that with higher values placed on an additional amputation-free life-year (e.g. > £50,000) the probability that surgery is cost-effective is less than 0.6.

FIGURE 25.

Incremental net benefit of a surgery-first strategy. Cost per amputation-free life-year calculated over 7 years.

Relationship between differences in cost and differences in overall absolute and quality-adjusted survival

Similarly, (Figures 26 and 27) incremental cost-effectiveness analyses can be undertaken in respect of OS (to 7 years) and quality-adjusted OS (to 3 years). As suggested by the point estimates, the cost-effectiveness of surgery compared with angioplasty is lower when these health end points are assessed. This is particularly the case when incremental costs of surgery are compared with the incremental gain in QALYs (calculated over 3 years only) where relatively large values have to be placed on an additional QALY before a surgery-first strategy could be regarded as a cost-effective use of resources. The confidence interval surrounding all values of cost-effectiveness also includes negative values reflecting the uncertainty and imprecision of the estimates and the relatively small incremental health gain when surgery is compared with angioplasty.

FIGURE 26.

Incremental net benefit of a surgery-first strategy. Cost per life-year calculated over 7 years.

FIGURE 27.

Incremental net benefit of a surgery-first strategy. Cost per QALY calculated over 3 years.

HRQoL

As expected, both the generic and disease-specific HRQoL of the BASIL trial cohort was very low at baseline. 67–71 No clinically significant differences between the two trial arms emerged across a range of generic and disease-specific HRQoL measures. 72,73 However, as suggested above, HRQoL data do have limitations and have to be interpreted with caution in the context of an understanding of the clinical realities for this group of high-risk and highly morbid patients. 74–77 The response rates were low (equally so in both trial arms) beyond 12 months; this is disappointing but perhaps to be expected in this patient population. Responders were more likely to have their trial leg intact and, presumably therefore, to exhibit higher levels of generic, but especially disease-specific, HRQoL. 78

Although patients have a very low HRQoL before treatment, surgery and angioplasty have very similar effects on short-term gains in HRQoL, which appear to be sustained for at least 36 months following randomisation. This plateau effect may reflect the fact that the aggregate data are conflating two very different groups of patients: those who keep their legs and those who do not. 79–85

As others have found,86,87 the relative clinical and haemodynamic advantages and disadvantages of a surgery-based versus an angioplasty-based strategy for managing SLI due to infrainguinal disease may not be easily distinguishable by means of generic or disease-specific HRQoL. 88–95